The manuscript is very well written, clearly structured, generally very well illustrated, and covers an highly interesting topic. The presented results are original, novel, and based on an innovative approach. However, before publication can be recommended, the following should be addressed:

Title, abstract, and elsewhere:

The terminology is somewhat unclear. The term ‘microclimate’ usually refers to the conditions (T, RH, prec) in the direct and closest environment of a wooden item. MC and T over time are usually named ‘material climate’, i.e. the conditions inside the material. The hierarchy is global climate – macro climate – meso climate – local climate – micro climate – materials climate. Suggest to adapt the terminology (see also numerous publications on ‘decay modelling of timber structures using this terminology in accordance with ISO standards, e.g. ISO 15686 series).

General comment / Introduction:

During the last approx. 20 years. Research developed parallels in wood material science and forest ecology. Decay models were developed for timber structures in use (above ground and in soil contact) as well as for deadwood and debris. The intro would significantly improve if similarities and differences between the two approaches would be highlighted.

E.g. the hypothesis formulated in L 72-74 has been shown to be correct by different studies in the field of wood material science (e.g. lab tests with pine blocks performed at VTT, Finland, and calorimetry measurements at Lund University, Sweden).

L9 and 89: Has it been Radiata pine sapwood? Please clarify.

Figure 2: The colour scale is hard to interpret. Differences in colour between the test sites are hard to distinguish (even for me, and I am not colour blind).

L 94: Unclear what is meant with ‘treatments’. Is it the application of the mesh? Treatment of wood usually refers to a coating or impregnation with repellents and biocides.

L 128: What is meant with ‘intact wood’? Is it non-decayed wood? The wood MC will drastically differ between decayed and non-decayed wood – how has this been considered?

Section 2.2.2:

It stays unclear how the dimension of deadwood components can be considered.

L 183 / 192: Unclear what fuel moisture sensor is referred to.  What kind of sensor? Where installed?

Figure 6: Species codes should be explained in the main text, not only in the supplementary material.

Discussion, L 303 ff:

The discrepancy between measured MC and predicted FMC is especially prominent at high moisture levels. Isn’t it most likely that this is explained by the geometry of the wooden elements. The effect of capillary water uptake must have been a multiple in the small (more or less cuboid wood block) compared to ‘normal’ deadwood forming long cylinders. Should eventually be included in the discussion.

General comment / Discussion:

The link of the presented models/ simulations to the physiological needs of the decay organisms involved is somewhat lacking. Numerous decay models have been developed in Europe and Australia (e.g. at CSIRO) to describe the relationship between wood decay, climate, and a couple of other impact factors. How does all this relate to the findings of the recent study?

Overall, the manuscript is well-written and easy to follow.

However I have a few issues with wood moisture/temperature modelling that I feel should be addressed.

The largest issue here is that, looking at Figure 3, it’s not at all clear to me that the model simulates the observed wood moisture and temperature. Providing the data as time-series, as is done in Figure 3, makes it difficult to assess the model skill. Moreover, nowhere in section 3.1 do the authors provide any model skill statistics (e.g., bias, R^2, RMSE, etc). Judging from figure 3A, I would guess that these statistics would not be very promising. As well, the comparison of air temperature and wood temperature in Figure 3B is not very illustrative for the purpose of model validation. I would want to see a comparison of simulated wood temperature and measured chamber temperatures, which the authors take as a proxy for wood temperature.

For this manuscript to hold together I feel like the authors should show that the wood moisture/temperature model has a reasonable amount of skill.

Another issue (that I believe may be a cause of the poor model skill) is the fact that the authors train the wood moisture/temperature model on a standardized fuel stick, but then apply the model to wood blocks with different dimensions. This may be problematic because in van der Kamp et al (2017) when the model was fit to different sized sticks, the optimal parameter set changed, suggesting that there was no one parsimonious model that could be applied to a piece of wood of arbitrary size. Indeed the authors found the need to re-adjust the m_max and f parameters.

This brings me to my next major point: Why not attempt to use the van der Kamp model to simulate the observed wood block moisture values directly, and avoid the step of modelling the automatic fuel stick first? It’s not clear to me that this approach would result in worse model skill than what’s shown in Figure 3.

SECONDARY ISSUES:

One secondary issue that the van der Kamp model assumes that the stick is elevated above the ground. However, in this study the sticks were sitting on the ground. The main issue with this discrepancy is that for the low wind regime of a subcanopy sites, the aerodynamic resistance of an elevated fuel stick is likely going to be less than for a stick sitting on the ground; moisture and heat are more easily transported to and from an elevated stick.  However, your model calibration likely implicitly corrects for this by decreasing the internal diffusivity to compensate for the inflated aerodynamic diffusivity. Indeed, your optimized bulk diffusion coefficient is an order of magnitude lower than the values  found by van der kamp et al. If you do use the van der Kamp model for simulating wood on the ground, I would hope to see this issue at least mentioned in the manuscript.

Another issue is the fact that the authors normalized the automatic fuel stick data to remain within the range of operating range reported by Campbel Scientific. I have read numerous articles that use the CS506 sticks, and have worked with these sticks myself, and I’ve never come across such an approach. Is this something Campbell Sci recommends? Unless this is something Campbell Sci suggests, or if you have a defensible, physical reason for doing this, I would recommend avoiding this step.

Another issue with using the CS506 sticks that isn’t mentioned here is the fact that individual fuel sticks have consistent biases when compared to each other (see section A.2.2 of van der Kamp, D. W. (2017). Spatial patterns of humidity, fuel moisture, and fire danger across a forested landscape. The University of British Columbia). The mean biases between sticks are often on the order of a few % moisture content. Again, the model calibration would probably compensate for this bias as the authors undertake a separate calibration for each stick. However, these models would likely lead to wet or dry biases when applied to the different wood blocks.

I have a few smaller points. Firstly, the use of a sum of squared errors as a model evaluation metric seems odd to me. Why not use something more common, like RMSE, or MSE? Also, the fact that the metric is a sum and not a mean is confusing. Wouldn’t the SSE metric therefore be dependent on the number of datapoints available? That seems less than ideal for a model evaluation metric. Also, a sum of errors doesn’t really mean anything that intuitively makes sense physically. Finally, equation 9 defines SSE, but why is there an error_i term as a denominator? is the error_i equal to simulation_i - observation_i? If so, this just ends up being the square root of the sum of the errors. I've never heard of a "sum of Squared errors" being used as an objective function for model calibration.

Finally, A brief description of the weather dataset would be helpful. the Duan et al., 2023 reference doesn't seem to contain a very detailed description.