[I've reviewed the same manuscript before. As far as I can see (main conclusions are unchanged, figures are identical), the mansucript version under review at here is identical to the earlier version I have reviewed. Therefore, I am posting my previous report here again.]

This paper investigates trends in global leaf area index (LAI) and attributes them to drivers (climate, CO2, land use change) based on factorial simulations with a set of DGVMs and a fully coupled Earth System Model. This is basically a revisiting of a study published earlier (Zhu et al., 2016 NatCC) that applied the same approach (model-based attribution of drivers) and used the same LAI product (GIMMS3g, based on data from the AVHRR mission; Zhu et al. also used GLOMAP and GLASS to obtain more robust results).

Winkler et al. reach conclusions that have potentially high relevance for our understanding of global vegetation dynamics in response to climate change and (in particular) to CO2. Effects of rising CO2 remain a major uncertainty in Earth System Model projections, owing to challenges in observing and attributing effects. Hence, deriving new insights from available observational records is needed.

The paper by Winkler et al. is well written and display items are of high quality. The fact that their conclusions directly challenge findings by Zhu et al. (2016), although relying on largely the same method and data, caught my attention. Winkler et al. write in their abstract ("Our results do not support previously published accounts of dominant global-scale effects of CO2 fertilization.", l. 16) and in their conclusions ("A cause-and-effect relationship between CO2 fertilization and greening of other biomes could not be established. This finding questions the study by Zhu et al. (2016) that identified CO2 fertilization as the most dominant driver of the Earth’s greening trend.", l. 722), and in the Key Points ("Most models underestimate the observed vegetation browning, which could be due to an excessive CO2 fertilization effect in the models.")

Strong conclusions require strong evidence. However, I have several strong concerns with how these conclusions were reached. In my view, the evidence presented here does not support this main conclusion (represented by the three citations I refer to above). Although I'm convinced that the analysis itself is diligently carried out and I consider that the paper offers a valuable discussion of the wide and relatively recent literature on the topic, I am concerned that the main conclusion will not meaningfully contribute to advancing the field. My concerns revolve around two main points:

1. Winkler et al. rely on a single LAI product to derive trends. Yet, several papers have documented inconsistencies between greening and browning trends between satellite data products. In particular, the product used here (LAI3g) is based on data from the AVHRR mission. It has been reported that respective data is affected by orbital drift of the satellite (Tian et al., 2015) and sensor degradation (Piao et al., 2019). The MODIS Collection 6 does not support the AVHRR-derived browning trends in several regions (see also Chen et al., 2019). This affects in particular North American boreal forests. The AVHRR-based browning seen in this region combined with the apparent failure of models to capture the same trends has been used by Winkler et al. (with a largely over-stretched logic) to argue that CO2 effects were inappropriately represented in models ("Thus, it is important to focus model development not only on a better representation of disturbances such as droughts and wildfires, but also on revising the implementation of processes associated with the physiological effect of CO2, which currently offsets browning induced by climatic changes.", l., 744). This is non-sense both in view of the known lack of robustness of apparent browning trends, and in in the logic of the argument itself. The failure of models to capture a browning trend may also be due to insufficiently sensitive responses to climatic drivers; and in this case (North America) is most likely due to inappropriate representations of disturbance in models (Anderegg et al., 2020 Science).
2. One aspect that distinguishes the study by Winkler et al., from that of Zhu et al. (2016) is their probabilistic driver attribution. As the authors write, the method has been adopted from Pearl et al. (2009) and Marotzke et al. (2019) who applied it to attribute drivers of near-term climate change. However, I consider that the application of this method to investigate drivers of vegetation change is ill-conceived. The usefulness of probabilistic attributions is evident when dealing with systems that are characterized by a substantial inherent stochasticity (deterministically chaotic systems). In such cases, simulated variations are not necessarily forced, by may result from unforced internal variability. This is not the case for vegetation dynamics, where the (simulated) internal unforced variability is typically zero (except for some models, e.g., LPJ-GUESS, that simulate stochastic gap formation, or some relatively small internal variability arising from stand dynamics - which are actually not simulated explicitly at the individual/cohort level in TRENDY models). This actually facilitates driver attibution. All simulated trends are uniquely attributable to drivers using factorial analyses. As a consequence of relying on a probabilistic attribution, Winkler et al., find, e.g., no clear attribution in some semi-arid regions (Africa, South America, AUS) (l. 680-690) due to high interannual variability of green vegetation cover. As I read the paper by Winkler et al., such findings underlie their conclusions (e.g., "We find that CO2 fertilization is an important driver of greening in some biomes, but not dominant globally as suggested previously", l. 126). I would argue that the findings by Winkler et al., do not provide new insights that allow for a revision of findings by earlier studies (e.g., Zhu et al., 2016), but rather fail to identify drivers (including CO2 effects) due to their application of an inappropriate attribution method. In most other biomes, attributions made here are largely identical with attributions made by Zhu et al., 2016 and also summarised by Piao et al., 2019.

I regret that I cannot offer a more positive assessment of this manuscript. However, my review should not discourage authors to use their results for a revised manuscript, where more attention is paid to assessing robustness of greening/browning signals in the context of multiple satellite products, and where caution is applied when reaching conclusions based on absence of evidence following the attribution method ("Causal Counterfactual Theory") applied here, and claiming evidence for an overestimated CO2 effect in the current generation of terrestrial biosphere models.

[Text in italic was not in my previous review report.]

The manuscript by Winkler et al investigates drivers of global LAI trends using a mix of long-term observations from AVHRR combined with Earth System Model sensitivity runs to provide causal attribution. The manuscript is in general well written and the results interesting and of general scientific interest. Please find some comments/questions below:

Title: I am not convinced the title conveys the gist of the paper, in fact I find it somewhat misleading. It reads as if the slow down of greening is driven by a further rise in CO2. The word "instead" instead of "with" would have made more sense but then again, the authors would have to make the topic of the title the key message of their paper, which it isn't (and it is hard to attribute to a weakening CO2 fertilization effect anyhow). For this, the author would have to use their counter-factual theory on the change in LAI changes between the beginning and end of the time period.

That said, it would be necessary to also discuss the results of Wang et al (Recent global decline of CO2 fertilization effects on vegetation photosynthesis) in the current manuscript as it is related to trends in CO2 fertilization as well (especially a reported decline of it, which differs strongly from Trendy).

One main strong statement of the paper is that it challenges finding by Zhu et al in 2016 (with some shared co-authors!). It sounds like a strong statement early on but if I look at Figure 3, I would say that the CO2 fertilization effect appears to be dominant at the global scale (despite some regional variations). It expands and adds nuance to Zhu et al, but challenges is too strong a word in my mind. There is enough material in this paper to warrant publication and no need to over-emphasize differences wrt to a previous publication.

Browning Trend in 2000-2017: When I look at Figure 3B, it appears a lot of the apparent browning trend in the later time-period is driven by a sudden decline in the relative change in years 2015-2017. What happens if you omit these years from the investigated time-period? What might cause such a sudden decline that might be related to the effects of CO2 fertilization or Radiative Effects? If this is related to detector issues or years with strong internal variability, I would remove these years (as long term drivers appear unlikely to suddenly appear). In fact, models and obs seem very consistent with each other between 2000-2014. As far as I can see, most discrepancies might be due to years 2015-2017 but I might be wrong. A critical discussion would be required here. Surprisingly, I couldn't find these strong effects of the last 3 years in the SOM plots, was it specific to some areas only? Can it be checked against MODIS data as well, which could be more reliable now? In fact, the first few years in Figure 3B are also VERY small, so you are fitting a linear trend through a time-period in which both ends are highly unusual. This can heavily bias derived trends, please evaluate and discuss the impact of chosen time-periods for trend analysis critically. https://doi.org/10.31223/X5K89V outlines some concerns I have with respect to AVHRR and the application to look at small changes (beyond pure trends). Please answer all questions in this paragraph.

A more general question regarding vegetation dynamics and CO2 fertilization, as you mention "as thoroughly equilibrated global carbon cycle" on line 192: What are the time-scales in ESM for CO2 fertilization? At the leaf scale, the gain in GPP is immediate but if you consider LAI, CO2 fertilization might cause a new state, which won't be achieved within a year, especially if species compositions will be affected. I would be curious what time-scales the models predict. E.g. if you changed CO2 suddenly but kep it at a higher level, how long would it take to run the carbon cycle into a new steady-state? I am mostly asking because the CC was certainly not in equilibrium in 1980 as CO2 increase and human land impacts are constantly shifting the needle. How much of the greening effects would have occurred (persisted for a while) even if we had suddenly frozen the CO2 levels at the 1983 mixing ratio and how would these "legacy" effects affect your overall conclusion? This is not a strong criticism but rather scientific curiosity.

Causal theory: One caveat that could/should be added is that this is only valid if the models, which are the basis for the sensitivity runs, are representing the truth. E.g. for the browning trend, you would actually find NO causal attribution from models alone, is that right?

  Line 36: Stomata can even respond at short time-scales when CO2 changes, stomatal density or max conductance takes time to adapt. (you mention "in time").

Line 88: "not dominant globally". Again, I am having difficulty to not see a similar effect in Figure 3c. In line 421, you even say so yourself. I am a bit lost here.

Line 449: weaken->weaker

Sections 3.10+: I was just a bit confused as the discussions now move from causal theories to more local descriptions, partially just citing other papers to explain specific events. It also shows the limits of your causal method as the lack of drought legacy effects (e.g. in tropics) can potentially bias your mode sensitivity runs. For some effects that you mention are due to RF, it would actually be interesting to separate out effects of CO2 RF into VPD, temperature and PAR effects (due to cloud cover changes), CO2 RF has various impact factors, which can very regionally in importance...

Overall, I would recommend revisiting the statements regarding Zhu et al, mention caveats in counter-factual theory using models as surrogate truth, investigate the impact of 2015-2017 on the greening/browning trend in the later time-period