I welcome the opportunity to comment on the latest IGCC paper, before the deadline of 22nd June 2025.

The Indicators of Global Climate Change reports are ambitious. However, to be of value to "evidence-based decision-making", they need to be more robust about presentation of uncertainties, dataset choice, and differences of opinion. 

This study would be much more useful for other scientists and policy-makers if it did not try to link itself to the IPCC assessment cycles so closely. 

The studies have gone through much less review than IPCC reports have.

While the authors have tried to follow FAIR principles - like the IPCC - there are too many cases of data and code not being publicly accessible.

It seems arbitrary which IPCC methods are followed "as closely as possible" and which are modified or completely new. 

Inconsistencies between the IGCC studies for results of the same periods make it difficult for anyone to "Track ... between IPCC report cycles". Many differences in "updates" for latest year/decade will be due to changes in method and data source, and may not be as representative of climate change as is often suggested. 

AR7 could be hindered if there is an attempt to force a continuation of a later IGCC paper with it. 

Using terms like "WGIII update" & "IPCC update" give impression this is an official IPCC update, when it is not.

In below:

F23 = Forster et al. (2024) ESSD

F24 = Forster et al. (2023) ESSD

F25 = Forster et al. (2025) under review with ESSD

General comments

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* FAIR principles:  Not all code for producing the figures is available. The github and zenodo links are somewhat confusing with discrepancies with what is in Section 13 and what is in the references. Dataset version numbers are not always given. There are no direct links to datasets within the manuscripts. It looks like the authors expect readers to hunt throughout the github/zenodo links to find the links. These links are not easily found ... if at all. There are mistakes in some of the repositories, which have been there since F23. 

* Lack of uncertainties 

There seems to be an increase in the number of values being presented without any uncertainties, over what was in F23 and F24. 

For instance, no uncertainties are given for the observed temperatures for 2024 anywhere in the paper, despite it being a prominent result.

Various statements are not supported when consideration of the different sources of uncertainty are accounted for.

* Inconsistencies for results from report to report

How can one interpret differences in results for the latest year/decade between reports, when values for the same periods change from report to report? e.g., 

1) First five columns of numbers in Table 1 are different to values for the same periods in Table 1 in F23, Table 1 in F24 and with the rows of three of the periods in Table 2.1 in IPCC AR6 WGIII.

2) Values in Table 2 for "2019 (updated)" differ from those for "2019" in table 2 in F23 and table 2 in F24

3) Values in Table 6 for "repeat calculations" for 2010-2019 and 2017 differ from the "repeat calculations in F23 (table 6) and F24 (Table 6)

4) Table S2 has subtly different concentrations, for same years in F23 (table S1) and F24 (Table S2) 

* New science

In various places new analyses are presented. These really should be presented in separate studies, to allow a full peer-review assessment to take place. 

e.g., the analysis in Figure 8, the method to estimate volcanic forcing in 2024 (SI S5.5.2), or the analysis in S7 "2023 and 2024 temperature anomalies".

There also appears to be a lack of consistency with assumptions, choices and data used in some of these new analyses differing to what is used in the rest of the paper.

* New volcanic forcing

The volcanic forcing in Figure 5 looks quite different to figure 3 in F24. It is due to a different volcanic forcing dataset being used. The proposed CMIP7 dataset has not yet been peer reviewed, and given the very different methods to construct it, there are questions which really need to be addressed before it gets used in anger. e.g., The aerosol distribution following the Mt Agung eruption was robustly observed to be mostly in the Southern Hemisphere, but the dataset has a pretty much hemispheric symmetrical distribution.

* Aliasing

When comparing results for adjacent overlapping periods it is harder to interpret the results than the authors suggest, due to aliasing. The significance of such changes should be treated cautiously.

e.g., In Section 7.1 and table 5, interannual variability projects onto the differences between overlapping 10 year means.

The reported 0.15C increase between 2011-2020 and 2015-2024 is actually half of the difference between 2011-2014 and 2021-2024, so has more "noise" than differences between non-overlapping 10 year means.

* Kadow GMST observations

It is astonishing that an observational temperature dataset is still being used that has not been documented (there is no paper/report describing the Kadow model using the HadCRUT5 observational dataset), and is not publicly accessible. 

* Human-induced warming attribution

I continue to be troubled by the lack of a presentation of the strength/weaknesses of the different methods. 

They all use global mean temperatures, GWI - monthly or annual means, KCC - a mixture of multidecadal and annual means, ROF - five year means. This means statistical over/under fitting is of concern and interpreting similarities and differences between the results of the different methods challenging.

The GWI method uses a simple model but with no attempt to assess over/under fitting, which is more prone to end-effects than the authors claim, and so it is difficult to understand whether the fit is just a coincidence.

The ROF method uses an approach that effectively has to trade off between variance and bias in its estimates of the climate noise covariance matrix. In normal uses of the method a residual consistency test is done to see if some measure of over/under fitting is noticeable - although that is not discussed in the manuscript (if it was done).

The KCC method assumes that the model responses and observations are interchangable, and uses a residual of model responses subtracted from the observations to deduce noise characteristics, so in effect starts out with an assumed anthropogenic and natural attribution. It also assumes the anthropogenic component of the forced response is just the smoothed part of the historical (anthropogenic and natural) response, thus any multidecadal natural responses present will contaminate the "anthropogenic" response used. 

Fundamentally the net anthropogenic attribution is less informative than the authors portray. All the methods will end up with attributed anthropogenic trends that track the observed trends, as long as long term trends of natural responses is small (Section 6.1.2 in Allen et al, "Quantifying anthropogenic influence on recent near-surface temperature change", Surv Geophys (2006)

"We are fitting all model-simulated signals to the same data so it is not surprising that, after the fitting is done, the scaled model-simulated responses are brought into agreement with each other.") The wider divergence of attributed GHG and OHF supports that view (Figure S8). Including spatial information, could help in gaining confidence in the results, as discussed in Allen et al. 2006. 

All statistical model/observation analysis methods have different strengths and weaknesses. It does not mean they are perfect, or that they are not useful. Without giving a more fuller context it is not possible for a reader to interpret the results in an informative way.

Specific comments

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L93 No uncertainties are given. If they were it would challenge the "well above" statement. 

L137 Not all the data is available in the zenodo repository. Some links are there but not to all of the datasets e.g., one of the observed GMST datasets, precipitation, sea level, GHG concentrations ...

Figure 4 top panel, missing N2O label on y-axis.

Table 2 Are the values in column "2019 (WG1 for ERF estimates)" correct? They appear identical to the F24 table 2 "2019 emission" column. I tried to find the "WG1" values in AR6 but couldn't find them. 

L502-513 Given the later deep dive into trying to assign causation to year-to-year changes, it seems curious that changes from year to year in natural forcings are glossed over here.

L512-513 The volcanic forcing is not negative according to figure S2, just less positive than recent years.

Section 7.2 and elsewhere. No uncertainties are given for the 2024 GMST value of 1.52C. F24 give uncertainties of about +/-0.1C (90% range).

L 634-635 Given F24 reported uncertainties on GMST of +/-0.1C, it is not "likely" that 2024 is warmer than 1.5C, but rather "as likely as not" - using IPCC convention.

L641-642 Attribution has not been discussed yet, so a reader might be unaware that the "human-induced warming" estimate has a "likely" uncertainty range of 1.1C-1.7C (Table 6). If that is accounted for then the probability is not "1 chance out of 6",  but approaching 1 in 2.

L642-644 and Figure 8 I could not find the exact same "framework" in IPCC AR6 WG1 chap 3. Cross-chapter box 3.1 is close, but that does not mention "anthropogenic global warming levels". I do not follow what is being done here. This really needs to be in a study of its own, to get closer attention.

Figure 9 Giving the observed warming for 2024 on the right hand side would be nice.

Table 6 Observed first column for "2010-2019" has different uncertainties to that "Quoted from AR6 Chapter 3 Sect. 3.3.1.1.2 Table 3.1" Observed final column "2024" has no uncertainties. It appears the last two columns are "trend-based" (table S5) but equivalent columns in F23 (table 6) and F24 (table 6) are "single year". 

Figure 10 is very different to figure 8 in F24. Bizarrely the natural changes are smaller than shown in F24.  I don't understand how this is the case, especially given the amplification in volcanic forcing (Figure 5).

Section 11 "Global Land precipitation"  How was the GHCN v4 dataset processed. It is provided as station measurements, and not as a gridded dataset. How this is processed is important.

Figure 12  This looks very different to figure 2.15c in AR6 WG1. The change in climatology period is having a striking impact on the evolution of the datasets that have unchanged versions. This should probably be noted.

SI L174 Durack 2025 is not in references, but if it is  https://egusphere.copernicus.org/preprints/2025/egusphere-2024-3729/ then that paper is a review of what happened up to CMIP6 and does not describe what is planned for CMIP7.

SI S5.5.1 and S5.5.2 I don't quite understand the reasoning behind the effort to try to update the volcanic forcing for 2024, but not the solar forcing. 

SI L191-208 Giving uncertainties for the reported values here would give helpful context about confidence in the values.

SI Section S7 the individual observation temperature dataset changes over the periods assessed are not given. This is important for understanding structural uncertainty in the observed trends. 

SI L322 - 384 "2023 and 2024 temperature anomalies" This analysis needs to be in its own paper.  Given the lack of update to solar forcing and the effort to update the volcanic forcing in section S5.5 it seems odd that here different estimates are used and relied on. In the main text (L487) it is stated that it is "problematic" to attribute year-to-year trends to aerosol forcing. How does that sit with what is being described here? Also I believe it uses a different observed temperature than elsewhere in this paper.

SI L322 - 384 "2023 and 2024 temperature anomalies" This analysis looks familiar. Might it be worth mentioning it has been published before (albeit it not in a peer reviewed journal). https://wmo.int/publication-series/state-of-global-climate-2024

SI L389 "combine measurements of near-surface temperature over land and in some cases over ice" There were no measurements of air temperature over ice, except in some very rare weather ship observations in Arctic circle.

SI L448 "some CMIP6 models may have unrealistically high decadal variability" ... and some will have low decadal variability! As we can't unambiguously observe it, we can't assess which models have realistic decadal variability or not.

SI S8.1 There are inconsistencies here about the importance of differences between GMST and GSAT with what is said in S8.2.1 and S8.2.2. It also rather simplifies the complexities of trying to account for the difference in models and observational datasets, especially over sea-ice when coupled models differ considerably in sea-ice coverage, and there are very few direct measurements of temperature.

SI L509 It might be worth mentioning that the "7%" increase in the best estimate of anthropogenic warming happened when HadCRUT5 had a ~7% increase in warming over HadCRUT4 for 2010-2019. This supports my earlier argument that net anthropogenic attribution is not as informative as we would like.

SI Table S4 how are the GSAT and GMST results identical for GWI and KCC. They both use GSAT from coupled models at some point. Section S8.2.1 and S8.2.2 try to claim that GMST and GSAT are effectively the same, despite what is said in Section S8.1 and S8.2.3. Can the authors make up their minds? ;-)

SI S8.3 I don't think it is explained how the GMST attributed results are estimated from the GSAT results.

SI S8.3 The results are presented against the assessed observed temperature changes, but the analyses were done using HadCRUT5. How much impact does this have?

The annual update by Forster et al. provides a valuable and timely assessment of ongoing climate change, particularly given the heightened attention on the sustained record global warmth, elevated Earth Energy Imbalance (EEI) and the questions over how aerosol, cloud feedbacks and internal variability are contributing, which are important to answer in regard to the magnitude and rate of near term climate change. I focused mainly on Sections 6 and 7.2 and provide some suggestions below including a number of relevant references that were not assessed. 

1) L546 Although EEI dropped in 2024 from a peak of nearly 2 Wm^-2 from mid 2022 to mid 2023, due to greater outgoing longwave radiation during the mature phase of the 2023/2024 El Niño, levels did not fall as low as previous mature El Niño evens such as 2016 or 2010 (Allan & Merchant, 2025 ERL doi:10.1088/1748-9326/adb448; Mauritsen et al. 2025 AGU Adv. doi:10.1029/2024AV001636).

2) L541 - the increased EEI corresponds with an accelleration of ocean warming, not merely an increase (e.g. Merchant et al. 2025 ERL doi:10.1088/1748-9326/adaa8a)

3) L551 -  We also showed the EEI increase to originate from increases in absorbed sunlight associated with clouds over the ocean, with hotspots over Californian and Namibian stratocumulus zones (Allan & Merchant, 2025).

4) L635 - is this an IPCC likely exceeded 1.5^oC? A recent WMO synthesis stated 1.55 ± 0.13 based on the 90% confidence range mostly relating to the 1981-2020 minus 1850-1900 IPCC offset applied. I think the 90% confidence range covers 1.645 standard deviations and the 66% level just below 1 standard deviation so this may also span below 1.5°C. "Likely" is probably fine but “More likely than not” (>50%) may be more correct. An uncertainty could be shown in Fig.7 or at least mentioned in the caption.

5) L651 - the probability of the large jump in global temperatures was increased by the fact the El Niño followed an extended La Niña 2020-2022 (Raghuraman et al. 2024 ACP doi:10.5194/acp-24-11275-2024)

6) L677 - the ocean surface warming is only reconcilable with the raised EEI if the mixed layer shallowed or was compounded by heat from the deeper ocean sequestered during the extended La Niña (Allan & Merchant, 2025 ERL). Shallowing of the mixed layer was liklely to have played a role in the Atlantic (England et al. 2025 Nature in press, published June 19th) while cooling in the 100-300m ocean layer implied a reversal of the downward heat flux below the mixed layer (Minobe et al. 2025 doi:10.1038/s41612-025-00996-z; Allan & Merchant, 2025). It is also likely that a smaller proportion of the EEI directly heated the ocean as more energy was used in heating the atmosphere and probably the land surface (Allan & Merchant 2025 ERL; Minobe et al. 2025).

7) L678 - see also England et al. (2025) Nature (in press) regarding the North Atlantic warming (due out 19 June)

8) L687 - also Allan & Merchant (2025) ERL relating to the mid 2022 to mid 2023 energy imbalance and the reduced absorption of sunlight over the cloudy ocean

9) L689 - for global temperatures to stabilise, the peak EEI and decades of decline are required (Mauritsen et al. 2025 AGU Advances, doi:10.1029/2024AV001636, Fig. 2) emphasising the importance of tracking this quantity and serious implications of the risk to the relevant observing systems

10) L1787 - repeated authors from von Schuckmenn et al. 2023 reference

11) Table3 - I was initially confused by the solar ERF estimate in Figure 5a being for a single year verses the whole solar cycle estimate used and assumed in Table 3. Perhaps a separate symbol could be used for the full solar cycle estimate (and updated to 2014-2024 or corrected for the solar cycle)? However, the single year value is useful since it does contribute a small amount to the larger EEI in 2024 (e.g. Hansen et al. 2025 SPSD doi:10.1080/00139157.2025.2434494; Merchant et al. 2025 ERL doi:10.1088/1748-9326/adaa8a). 

12) Section 8.2 - a couple of studies have noted that the level of annual warmth and the sustained warmth over many months makes it inevitabole that the 1.5 degree Celsius above pre-industrial thershold will be breached (Cannon 2025 Nature Clim. 10.1038/s41558-025-02247-8; Bevacqua et al. 2025 Nature Clim. doi:10.1038/s41558-025-02246-9) without a drastic increase in mitigation (or a large explosive volcanic eruption) so this could be mentioned.

13) Section 8.3 could also consider Samset et al. (2023) Comm. Earth Env. doi:10.1038/s43247-023-01061-4 and a preprint by Rahmstorf & Foster doi:10.21203/rs.3.rs-6079807/v1

14) Section 1 final paragraph - a bulleted or numbered list may work better for the reader to point to the many sections 

First of all, thank you for your work.



When I check the four observational datasets, I get 1.262 Celsius 10 years' mean anomaly instead of 1.244 for 2015-2024. The RCB comparison between both is huge. If we rely on Zeke Hausfather's estimate for 2025 (1.52), at the end of 2025, that ten years mean will be 1.304. That means we might deplete RCB for 1.5 Celsius (50% likelihood) already in 2025. 



Based on your dataset, for the next years' paper, you will still mention that we will have some RCB (around 40) while we will be in minus. I think this is a highly sensitive matter because policy-makers take your results into account (UNEP uses this study series for its Emission gap report). 



I think more discussion in this aspect is critical. We are racing with the time and facing record temperatures which change a lot of assumptions about climate science.