Dear authors,

many thanks for responding to the referee comments. This will be a rather long letter, hence here is the most important part first: I have decided that major revisions are needed before the manuscript can be considered for publication.

One reason this letter is rather long results from an unfortunate circumstance. You may have seen that initially 3 referees have accepted to review the paper, however, only 2 posted their review in time. After the discussion was already closed I have been contacted by the third referee that was unable to post the comments anymore. In this particular case (since referees 1 and 2 suggested major revisions and rejection) I was happy to have another opinion. You will find the additional referee comments at the end of this letter. I dont expect you to answer these additional comments point by point, but I would appreciate if you could incorporate them in your revised manuscript, indicating in the cover letter where the manuscript has changed in response. In case you have questions regarding the comments by referee 3, please dont hesitate to contact me.

That said I noticed one common line between all referee comments (and my own judgement). All referees (including the additional 3rd referee) were excited about the topic and could see the potential. Unfortunately, at the same time all referees were unhappy the way the topic was presented. I think you have done a good job answering the referee comments, hence I will not go into details about the comments itself, however, I would like to point out that I intend to ask the same referees to review a revised version.

My decision to reconsider the manuscript after major revisions rests on the potential of the work. The referee comments may be substantial, even beyond major revisions, but I don't have the feeling they are impossible to implement. That said, if you do require more time than originally granted to revise the manuscript, please let me know and I am happy to grant a long extension.

Best regards,
Peter Landschützer

referee 3 comments:

I was initially excited to dig into this manuscript after skimming the abstract and seeing what it was about, but after doing so I must admit I did not find it to be especially compelling. I am very sorry to be so harsh here, but it is possible that I misunderstand the authors’ objectives, and I am certainly open to changing my mind about this manuscript.

I see three results here:

1. The ML methods reproduce the output ok (high R^2s, Figure 1). Ok, yes, fine, but this is totally boring & expected since you’re feeding them 60% of the data, which are presumably randomly chosen and therefore give fantastic coverage of the dataset. This is just a sanity check result, basically, but I count it for completeness.

2. The effective half-saturation estimates are sometimes good, sometimes bad. This is interesting but it seems pretty all over the place why it’s sometimes good & sometimes bad, so it’s hard to draw too much from it besides that, as the authors discuss, one should take effective half-sats with caution and many grains of salt, likely because of colimitation. However, if the authors are attempting to claim that ML methods can’t do a good job at this, the authors have to do a lot more work to show this; the results are based on pretty much all the default Matlab settings, there aren’t sensitivity results for these, there are other methods that might do better, etc. This is not a rigorous negative result, in other words.

3. In a highly idealized setting, random forests don’t get the intrinsic relationships right, while neural networks do. Beyond this, it pretty much falls apart. Again I find the lack of rigor in giving these methods and others a fair chance insufficient. Also, why not show the partial dependence plots in addition to what the authors have shown? Even if you like yours better, the PDPs can be illuminating. Moreover, I guess my main issue with this whole paper is that the authors really seem to be conflating apples and oranges when it comes to the equations at hand. Intrinsic relationships are typically growth rate vs. (concentration, temperature, light level, whatever). Apparent relationships are concentrations versus these. The Flombaum et al PDP for abundance vs. temperature shouldn’t look like the Eppley curve of growth rate vs. temperature. The authors make strict assumptions about loss rates (without explicitly deriving them) to try to match these up but this involves extra assumptions that are totally unrealistic including steady state and no feedbacks between trophic levels. And then when you integrate the intrinsic relationships over time and you include e.g. fluctuations in light, predator-prey cycling… of course the relationships are different. So the paper basically is just showing that except in extremely idealized contexts, and only then after making some strict assumptions to put things in the same units, intrinsic and apparent relationships between drivers and populations aren’t the same, when you try to find the intrinsic relationships with a couple of ML methods using their default settings. I don’t find this result interesting enough to warrant publication as it is.

Minor comments:

– The title could use some work, it is long and confusing.

– Abstract: ‘as little separation as hourly to daily’ sounds like you mean as low as an 1h separation between timescales – I’d use ‘versus’ rather than ‘to’ to be clearer. You don’t define MLR in the abstract, and it’s also not clear what you mean by ‘the limitations found by ML were overestimated’ – by whom?

– Reporting MSE & RMSE is totally redundant.

– Equation 1: Ok, fine, you can write the equation this way, but at least cite an example of someone using the starting differential equations so we know better where you’re coming from, if you’re not going to derive it yourself? Also see above; this is not an intrinsic relationship in my mind, because you have to make additional assumptions about other things, namely zooplankton dynamics, that have nothing to do with any given intrinsic relationship.

– I don’t understand why the authors switched the light portion of the equations from the different scenarios. Yes, you justify it & all as a Taylor expansion, but why not just use the same dependencies?

Dear authors,

many thanks for submitting your revised manuscript. The manuscript has improved substantially and is now ready for publication subject to some remaining technical corrections highlighted by referee#1 and referee#2 in their reports.

Best regards
Peter Landschützer