General comments:

Very interesting article on how estimate at high spatial resolution the evapotranspiration fluxes (ET) in the very heterogeneous urban canopy. The subject is important for the estimation of the runoff reduction in green space but also of the water need of urban green space.

The article is outstanding due to the diversity of estimation, with measurements (chamber as the reference but also soil water content) and modeling (empirical-statistical as the reference but also a wide range of conventionnal formula).

The work is very clearly presented, with a very complete and rigourus methodology combining different aspects (shading, vegetation characterisitcs, statistical test, ...). The database with the characterisation of the site (soil, vegetation, topography, urban scene) and with the temporal series of different hydrological and meteorological variables is really interesting and outstanding.

The form is perfect, with clear text and illustration ; I do not have a look to the data (https://www.hydroshare.org/resource/ba487d9c6e4b473f88d8298499ee1c6d/), due to a lack of time.

Specific comments:

See the pdf file for specific and detailed comments.

I suggest "Minor revision" (rather than "accepted subject to technical corrections") because I suggest to add some details on the development & performance of the empirical model (adding a chapter in the Supplementary Information at least). The evaluation is presented positivly in two lines in the article (L284-285), even though the model is subsequently used as a reference throughout the rest of the article. It would be useful, at the very least, to show and discuss the observed/simulated scattergram at the basin scale, and, if possible, at the various measurement points as well. 

Three other points could be add in the discussions part:

- the spatial role of other micrometeorological conditions than the radiation, for example the wind or the VPD ? Do you have some site informations of these variability (contrast in the two weather station for example) ? For another work, it could be possible / interesting to introduce such spatial variables in the empirical model ?

- At different lines in the article, the validity of conventional models (=formulas) is debated in terms of whether or not they take water stress into account (for example, lines 427–429). Upon examining the soil water content at -5cm (Fig. 3d), I find that the values are not particularly low (and one would expect higher values at greater depths) and that it is not certain that ET could be limited by soil water availability. This hypothesis is consistent with the shape of the scatter plots between ET values simulated by the empirical model and the different formulas: for example, this relationship is highly linear for the PM formulas across all ranges of ET values (Fig7), including high values whereas for these high values one might expect more severe water stress to occur. In summary, I get the impression that ET water limited situations are rare in the database, and therefore that the reasons for the offset between the empirical model and the PM models must be sought elsewhere ;

- The linearity of the relationships between the empirical and PM models, which consistently involve a simple offset, is truly impressive. A theoretical comparison of the two models could be useful for analyzing the following observation:

+ the empirical model uses the following explanatory variables: topography (via a 1/0 index), vegetation height (spatial variability only?), VPD (temporal variability only?), solar radiation (spatial and temporal variability), and soil moisture status (temporal variability at a single point); it is statistically calibrated on 7 x 11 daily ETs;

+ PM formulas primarily use the temporal variability of solar radiation, VPD, wind, and temperature, with a constant vegetation height.

So, for example, the effect of wind is taken into account in PM (via its aerodynamic term), which is not the case in the empirical model. Could this be a source of overestimation of PM ET ?

I welcome the authors efforts to address this complex challenge. The work provides valuable real insights into the heterogeneity encountered when attempting to characterise bioretention basins. The chamber data and spatial characterisation of the basin are valuable and useful contributions to science in their own right.

I feel the paper should be published subject to the following comments being addressed:

The naming of the three approaches, e.g. in the abstract, does not seem to be as precise and unambiguous as it could be. (1) and (2) both refer to ‘empirically-based estimates’ (vague), and could perhaps be better distinguished by specific reference to (1) chamber measurements undertaken at multiple locations and (2) a single vertical profile of measured soil moisture content.

The development of the statistical model (1) – Section 2.5 – is difficult to follow and not particularly transparent. The parameterized model, i.e. the final selected regression coefficients and parameters, should be clearly presented in the main body of the paper (e.g. within the Results, Section 3.1).

Define R²_marg and R²_cond.

For completeness, (for readers unfamiliar with the use of chamber experiments) please state how ET in mmol m^-2 s^-1 is converted into ET in mm day^-1. This could be included in the Supplementary Material.

I can see the value of comparing ET estimates based on soil moisture measurements against the chamber experiments, but I don’t understand the logic of deliberately trying to capture the heterogeneity with the chamber experiments compared with sampling at only one location with the soil moisture sensor. This is not really comparing the two measurement techniques, rather it’s comparing two spatial sampling approaches while also varying the measurement technique! Why did you not use multiple soil moisture sensors to better understand the localised variations in ET? This also leads to some speculation around line 346-7. The authors have noted that multiple sensors would be better (Line 350-351), but this doesn’t remove the question around experimental design. Consider simply introducing the soil moisture measurement approach as an order-of-magnitude sense check to the chamber-based model.

I am confused about whether/why moisture stress factors were, or were not, included in the application of the conventional models, Section 2.8. For FAO PM, normal practice would be to apply a water stress factor to the reference ETo in order to estimate actual ET. However, the commentary in Section 3.5 suggests that you did not include water stress. It looks as though (Supplement 3) you (potentially) included soil moisture content in the development of your empirical model, but then excluded it from your comparisons against the conventional ET models – I’m not sure that this is a fair comparison.

I understand that you have used K_L as a calibration coefficient to scale the estimates from the conventional ET models to better match your chamber measurements. I believe that the values ranged between 0.5-1.0 (Line 393). Please refer to Table 3 at this point in the text, as the actual values are easy to miss within the table.

The additive correction does not seem to be well justified or transferable, and could potentially lead to negative ET estimates. Is there a precedent in the literature for doing this? This is likely to be quite case-specific and not generally transferable. The reader can already see the offsets in Figure 7. It would be more useful to explore whether the inclusion of moisture stress factor addressed some or all of the overprediction observed with the conventional models.

Lines 464-466. Again a request to actually share the fitted statistical model so that the reader can see for themselves how ET varies explicitly with plant height.

Minor corrections:

• Line 25 – ‘align with ours’ should be ‘align with the ET estimate based on the chamber measurements’.
• Line 67 – ‘such multiplying’ should be ‘such as multiplying’.
• Line 106-108 – where exactly is the ‘rocky gabion’? What do you mean by ‘above’, ‘below’ and ‘lower’ in this context? Are these relative elevations, or upstream/downstream or north/south? Please also check lines 170-171 re the use of the terms lower and upper.
• Line 247 – should ‘raw time of solar radiation’ be ‘raw time series of solar radiation’. I don’t think you adjusted the time.
• Do ‘tall’ and ‘short’ (Table 1) equate to ‘large’ and ‘small’ (Figure 2)?  Please use consistent terminology.