This manuscript explores an important question in forest ecology: how disturbances alter the growth-survival trade-off across a broad set of North American temperate tree species. The authors utilised an impressive, large-scale dataset from the US Forest Inventory and Analysis (FIA) Program, focusing on variation in mortality probability (at zero growth) and maximum growth rate across 68 dominant species. The study also provides a novel insight into how forest developmental stage, taken as a proxy for disturbance severity, can constrain or even mask classic demographic trade-offs. While growth-survival trade-offs have been frequently investigated in tropical systems, applying this to broad-scale temperate forests and explicitly testing how disturbance might disrupt trade-offs is both novel and valuable.
The study is compelling and timely, but the manuscript can be improved by clarifying a few methodological points.

Comments and suggestions for improvement:
Methods:
The paper uses the stand developmental stage (basal area ratio relative to maximum BA for the local climate envelope) to classify “early” vs “late” stands, implicitly linking early-stage stands with disturbance. While this is a reasonable proxy, further elaboration or discussion of limitations would strengthen the argument, e.g., whether the stands definitely experienced severe disturbance, or whether they are simply in an early successional state due to other historical factors (past management practices). You could emphasise that “early successional” or “early developmental” stands are not a perfect measure of recent disturbance, but serve as an operational proxy for stands that have recently reset or remain in a younger structural state.
Regarding the approach used, it is not clear if you fully replicated the approach of Astigarraga et al. (2024), including the world climate and soil databases, or if you used some more regional databases on climate and soil characteristics. It also might be understood that this classification was just adopted from Astigarraga. Please, be more specific.
Moreover, regarding the use of the approach by Astigarraga in your study, nitrogen availability might not fully explain the forest stand's potential production (basal area). You might need to add more variables, such as pH, the clay, sand and silt proportion, or other relevant variables, for example, local topography. Otherwise, you could acknowledge that while climate and nitrogen data capture broad environmental gradients, local factors undoubtedly cause variation in “true” maximum growth.
In addition, converting a continuous stand development index (0-1) into two bins (≤ 0.33 = “early”; ≥ 0.66 = “late”) is convenient but not biologically supported; shifting the cut by even ± 0.05 can move dozens or hundreds of plots and change sample sizes, slopes, R², and p values. So, you might consider testing how stable the split into these categories is (a kind of threshold sensitivity analysis?).

The Discussion posits that disturbance filters out slow-growing species, but it would help to connect that more explicitly to real data patterns or references to documented mechanisms. For instance, do your data show a decline in shade-tolerant species in early stands compared to older stands?
A key pattern is the difference in species growth and mortality rates between early vs. late stands. The results show that a single species can have different demographic rates in these two contexts. Consider discussing whether these changes are driven purely by local resource availability (e.g., more light, open canopy) or differences in competitive interactions.

The study's major advantage is its large sample size. You might highlight the geographic scope (e.g., latitudinal range) or diversity of climate zones covered by the dataset.
Further, you mention that you excluded recently harvested or managed plots. Please, consider clarifying whether any stands might have had partial cutting or mild management in the past that was not recorded. If so, is there any potential bias?

The approach using the ratio between basal area (BA) and a maximum for the “environmental envelope” is sound. But it’s easy for readers to worry about the link between “low BA ratio” and “recent severe disturbance.” You should emphasise that although we cannot confirm the precise disturbance event, stands in the bottom one-third of the site-specific BA are typically younger or recovering from major disturbance. Moreover, consider briefly clarifying how big each cluster (environmental envelope) was and how you define that local envelope (i.e., how many plots in each cluster?). It might be well-detailed in Astigarraga et al. (2024), but a sentence or two might help readers.

Your dataset includes only trees with DBH over 12.7 cm, which is already big, especially for some environments. Do you think this might have affected your results? How and to what extent? You might consider discussing this sampling threshold. National forest inventories were designed to quantify forest resources at large scales and often do not reflect local specifics well.

I could not find information about the sampling years of the three NFI censuses from which the data were used. Please provide it in the revised version. Regarding this, my concern is that the specific climate between the censuses could bring further noise in the data. This becomes especially relevant if we suspect that mortality or growth might spike in drought years, or that overall growth could be trending upward across time due to CO₂ fertilisation.

Modelling species mortality:
Possibly mention how you validated model convergence.
If a small portion of species has borderline sample sizes (just at or near the threshold), it might be worth stating whether that introduces any bias.

Testing for Trade-offs:
The use of SMA regression is appropriate given that both variables have some inherent error, and you’re interested in their relationship rather than predictive modelling. I suggest that you confirm that data distributions do not violate the assumptions of SMA.

Specific comments:
Page 6, line 142: You refer to Table S1, but your supplementary starts with Table S2, so Table S1 is missing.
Figure 2: Consider labelling the x-axis as “Previous growth rate (cm yr-1)” for clarity.
Page 8, line 203-205: The increment between the 1st and 2nd census contributed to DBH at the 2nd census. Therefore, I suggest using the DBH at the first census instead.
Page 12, lines 280-281: You state that when analysing Angiosperms and Gymnosperms separately, the relationship between maximum growth and annual mortality at zero growth becomes weaker than when evaluating all species together. I suppose that this statement was based on the p-value. However, the p-value is higher because of the lower sample size (number of species in this case) after splitting the dataset into Gymnosperms and Angiosperms. So, I would disagree with using p-value as the measure of the strength of the relationship in this case. The SMA slope for Gymnosperms is lower, indicating a lower effect of maximum growth on the mortality. However, the SMA slope is not statistically supported.