General Comments:

This is an interesting paper that investigates the importance of lateral transfers of water and its effects on energy (mainly ET) within semiarid and complex terrain locations of Southeastern Australia. While not novel in addition of any extra model physics, it is an important addition to the scientific community that investigates land surface models and the bridge between hydrologic models. That being said, there are a number of comments and concerns that I have had while reading through this text. Specifically, I am concerned about the method that was used to bias correct precipitation inputs and the calibration period (which was only a length of 45 days). I would implore the authors to better support these decisions within the manuscript. Based on this initial draft, I would rate this as Fair on Scientific Significance, Good on scientific quality (mainly needing more justification), and Good on presentation quality and suggest major revisions to address comments below: 

Major Comments (in order of where they are in the text, not in order of importance):

Paragraph beginning on Line 103: Within this paragraph, the authors explain different overland flow and sub surface flows and how these and cannot feedback into soil water and energy fluxes. Please explicitly state what is meant here by lateral transfers (e.g. case 2b), and if the subsurface flow is still being parametrized despite the baseflow package being turnoff due to calibration. This paragraph is critical to understanding the scientific set-up of the study, and thus needs to be crystal clear.

Please expand, especially on the precipitation, the bias correction used. Is the idea here that you take a monthly accumulated rainfall at each grid cell from ERA5 land and the Australian Gridded Climate Data (AGCD) and scale each month to directly match the Australian Gridded climate data set? How does this effect the hourly precipitation rates? Infiltration rates will be highly sensitive to the hourly rainfall rates, so ensuring this is clearly explained is critical. See “Sampson AA, Wright DB, Stewart RD, LoBue AC. The role of rainfall temporal and spatial averaging in seasonal simulations of the terrestrial water balance. Hydrological Processes. 2020; 34: 2531–2542” for evidence showing that at hourly scale, rainfall is driving much of the uncertainty of infiltration, not necessarily the soil parameters (though these are very much still important).

Please provide information on the 45 day period that was used to calibrate the model. Were these high flow days? Were they low flow days? Why was such a small period of time (45 days aggregated by 3 days is 15 data points to calibrate on). More justification is needed. Specifically, why does it make sense here to calibrate to 3 daily flow (assuming accumulated), when the comparisons will be on monthly flow (accumulated as well?) I understand calibration is tricky, and am not advocating for the authors to do more work, but do think that justifying this choice somehow is necessary.

Figure 7: Please add a ET Change Relative to CTL label on the y axis. Also please ensure the labels are all correct (CTL1-250 doesn’t exist in this study).

Minor comments (in order of where they are in the text, not in order of importance):

Great introduction! I would contend that there could be a nod to some of the work that is being done in the Urban world with lateral transfers (understanding that this is not the scope of this paper, but is an important emerging area where hydrologic processes are just as important and often overlooked in LSMs). I would think a clear location to add would be in the paragraph starting on line 70.

Figure 1b): please change the outline color of the Upper Basins, Ovens, and Murray Riverina to something that isn’t blue. These are currently will be difficult to differentiate given the light blue color used for the terrain height being for much of the lowlands.

Somewhere within the manuscript or within an appendix, please list the specific choices made for the Noah-MP LSM in terms of physics schemes used. While out of the scope of this paper, these have a very clear influence on the results of the model, and should be listed.

Line 115: The “eight seasons” seems to be obfuscating the amount of analysis done. Why not just “2 years of results, broken into individual seasons” or something similar?

I am being pedantic here, but please define monthly streamflow; is this an average or an accumulation over the whole month? I assume it is an accumulation, but could not find it confirmed in the text.

Figure A3 panel a: why is there a single dot in the middle of the panel behind all of the text. Is this an erroneous plot? Also, please move the Bias and NSE results so that they do not overlap any of the lines. It is hard to read!

Please revise “ The simulated timeseries of ET are within the range from the DOLCE product most of the time, except in 6 out of 24 months where the simulations are slightly outside this range.” 25% of the time being outside of the uncertainty range is a pretty significant amount to be outside of the uncertainty estimates.

For ET in Figure 3: Please specify whether or not this is over the full domain in Figure 1b or just within the sub-catchments of interest somewhere in the text.

The results of this paper are significant for the hydrologic modeling and LSM communities, as they demonstrate the impacts lateral flow in LSMs and the possible implications for atmospheric fluxes. The methods of this manuscript are generally strong, and I anticipate that the results of this work could have implications for the hydrometeorological community.

However, I have some technical concerns on the methods that I ask the authors to clarify in order for this manuscript to be accepted.

Major Comments:

Section 2.1, Lines 100-110: I appreciate this discussion on the significance of horizontal routing with LSMs. I also recommend discussing the impacts of LSM depth, as the standard 2-m Noah-MP depth often does not capture groundwater processes and has resulted in dry biases with ET in some regions.

Section 2.2 and 2.3, Calibration: Please clarify why the authors use 3-day averaging for streamflow validation and calibration? This could likely underestimate major surface runoff events leading to flash flooding. Furthermore, calibration to 45-day periods may not capture the full range of processes that lead to hydrologic response. I recommend demonstrating that these parameters are consistent with a longer range calibration period. If this is not easily feasible within project constraints, I alternatively recommend discussing the assumptions and possible limitations behind this methodology decision.

Minor Comments:

Figure 1: Consider adding the channel network (even if it is only higher order channels) to help the reader visualize the hydrologic connectivity.

Section 2.2.1, Geographic Data: I find it surprising that the TERN dataset produced worse streamflow compared to the default soil dataset. Is this something that could eventually be improved with calibration?

Section 3.1.2, lines 215-220: The negative ET bias might reflect the limits of the 2m LSM. I recommend connecting back to this point in the discussion.