The authors measured the isotopic composition of water in an evaporation pan that was shielded against incoming precipitation. They compared their observations against theory and found that diurnal variations matter.

This is an odd paper. The subject is very old and well treated in the literature because evaporation pans were examined extensively in the 1970th to 1990th. The results mirror exactly theory and are deviating only if the theory is applied wrongly. The authors were not successful to convince me that there is enough literature that applies the theory wrongly to warrant publication of the data with such simple analysis.

There are some odd and formulations in the manuscript such as "rapid molecular exchange of isotopes between the water body and the atmospheric vapour, which predominates over the net isotopic effect of a simple evaporation process". This is a rather layman's notion that evaporation is a simple one-way process, which it is not. The old papers never assumed that. The authors could probably profit from reading some literature in plant sciences, for example Farquhar and Gan (Plant, Cell & Environment 2003), where this subject was treated extensively.

Their final remark "delta* [...] become detached from precipitation and atmospheric moisture isotopic content" is simply wrong. It is actually their Eq. (2) so it depends on isotopes of water vapour and it does not depend on precipitation. But it depends also on relative humidity and so might change even that one assume constant water vapour isotopes.

The authors do not really explain why they have decreasing isotopic composition at the end. But if the evaporating water gets more enriched than would be the actual new maximum enrichment given the new relative humidity, then it has to decrease. The way the paper is written, the environmental conditions are assumed very static, a priori.

So I was also astonished about the surprise that a average relative humidity is not appropriate. If one thinks about isotopic exchange, one sees that it is not relative humidity but absolute humidity (vapour pressure) that is relevant. So any other notion of relative humidity such as mid-day, ratio of mean vapour pressure over mean saturated vapour pressure, relative humidity weighted by saturated humidity, etc. would probably have been fine. If ever, one should probably use the Penman formulation rather than Penman-Monteith. The latte includes plants, the former does not.

I have not understood how the time series in the figures were constructed, especially when delta* was changing. Was delta_0 always constant? Did you go from one to the next observational time step? In latter case, I would have guessed that you could simply go one 5-min interval after the next and do not have to average anything.

So I would recommend publication if the authors would write down the dynamic theory, where their fraction of water volume that evaporated, i.e. evaporation, is calculated rather than assumed. This would probably be similar to Farquhar and Cernusak (Functional Plant Biology 2005) or any other non-steady state formulation of leaf water enrichment.

I would have a variety of minor to medium comments but I leave them out because I think the paper needs a thorough rewrite anyway.

This manuscript describes a field experiment to validate a classic model of isotopic evolution of an open water body under evaporation. The main conclusion—that time-averaging of micrometeorological parameters introduces bias—is a well-known phenomenon, as cited in the manuscript. The field data yielded relatively clean results and the analysis nicely illustrates the effect of time-averaging. The manuscript suggests that many other applications of this technique have done so inappropriately; I did not investigate all cited examples in detail, but at least one of them does not make such an error. Given that the time-averaging phenomenon is well known, the technical note is more of a reminder than a technical advance. If it is true that others are misapplying the technique and the goal is to correct that problem, I think would be important for the technical note to generalize the analysis a little more to illustrate the magnitude of errors likely to be introduced.

I think it is generally unfair to judge manuscripts based on what I would personally like to see done with data, so I offer the following comments in the spirit of suggestion for the future. Given that 5-min data are available, why not resolve isotopic composition at the 5 minutes and compare to the PET-weighting scheme? In theory the agreement between data and the model should be perfect and without imprecisions added during PET-weighting, and any deviations are likely to originate in micrometeorological measurements or assumptions about atmospheric vapor. I think these assumptions are more interesting than the time averaging because the time averaging problem is already well known. Do alternative assumptions about atmospheric vapor improve model fit? For example, are there systematic deviations of the model when there has been no recent rain?

L28 the cited papers did not all use weekly-monthly means.

L35 bidirectional exchange is ubiquitous, not just when humidity is high.

L45 isotope equilibration field studies have been conducted across a range of climates. The novelty of a subhumid climate is not great; e.g., the cited works by Gonfiantini include field data from Italy.

L67 it is a fine distinction, but the *expected* isotopic composition was modeled as Eq 1.

L69 Eq 1 is explicitly derived “assuming that the evaporation conditions remain unchanged” (Gonfiantini 1986, eq 7), so it is no surprise that it does not perform well at weekly timescales.

Fig 3 d-precipitation does not appear in Eq 2; I assume this should be d-A?

L100, L124-126, L129, L132 text duplicates figure captions with no additional information.

L105 apply how? weekly means?

L106 but there is a 4-week period when d18O was increasing in the pan while d* was less than the pan.

L108 because d* is completely theoretical and not a measured quantity, it is not clear why something “might” cause a decrease in d*. Why is there any question? Similarly, L109-110 is simply restating the theory being applied, with no original content being contributed by the experiment.

L111 there are no methods presented that would allow these mass balance estimates. Was the mass or volume of water in the pan measured each time? If so, please consider presenting those data instead of the calculated 16O mass. L114 suggests volume data are available.

L118 I suggest not using “RH” because “h” is already defined as the same thing.

L124 “d*18O” is not a concentration, it is a deviation.

Fig A2 the meaning of the solid lines is not specified.

L125, Fig 5, Fig A2 details of the methods to estimate PET are needed.

L136 relevant to what?

L138-140 I do not understand the point being made about rainfall and humidity and d*. It appears the sentence assumes something about the relationship between rainfall and isotopic composition of atmospheric water vapor, but their relationship is irrelevant to d* and only the vapor matters. It is of no importance to this statement that the isotopic composition of rainfall was used as a surrogate for the isotopic composition of vapor in this experiment.

L142 what is a “heavy isotope depletion period”? It is not clear which of the three nouns are being modified by “heavy.” It is also not clear what a “depletion period” is L143. Are these referring to periods when d18O in the pan become more negative?