This manuscript presents analyses of a time-series of EEI using satellite and in situ data, and compares it to time-series from Satellite (CERES) and in situ only estimates.  One issue with this manuscript is that the estimate is framed as being "from space geodetic observations" but the key IEEH parameter is estimated from in situ data of ocean warming.  Without those in situ measurement of ocean warming, the method would not be feasible.  This fact needs to be emphasized in the revised manuscript.  Also, in general, the in situ estimates are much more certain than the "space geodetic" estimate, which should be acknowledged more directly in revision. Given these increased uncertainties, more mention of what the "space based" method might add to the in situ method in the revision might also be helpful. Comments follow indexed by line number (L) where possible.

1. L9-10. The word "trend" is not a correct choice.  Consider changing to "mean value".

2. L10. The word "indicating" is not correct.  The mean value does not indicate an acceleration.  Perhaps change to "with an estimated acceleration of 0.29 W m-2 decade-1".

3. L23-29. In situ estimates relying mostly on Argo data are already there in terms of accuracy of 0.1 W m-2 on a decadal time-scale, at least starting from circa 2006 when Argo first achieved sparse near-global coverage. This fact should be indicated in the revised text.

4. L51-56. The Roemmich and Gilson temperature and salinity maps including mitigation against the influence of salty drifters that appear to be largely effective at removing the halosteric bias error.

6. L57-64. This is really the heart of the method, and reliance on Argo data to estimate the warming pattern and hence IEEH should be explicitly noted.  Without in situ data to show where (at what temperatures, pressures, and salinities) the warming is taking place, the method uncertainties would be unacceptably large.  So this is not really monitoring ocean heat content changes from space as the title implies!  It requires monitoring the changes in situ to work with any accuracy.  Also, ECCO is very poor at reproducing observed warming in the deep and bottom waters.  It shows global cooling from 1992-2011 (e.g., Wunsch and Heimbach, 2014, J. Phys. Oceanogr.)  whereas repeat hydrographic data (e.g. Purkey and Johnson, 2010) and Deep Argo float data show very definite warming in the global mean.

7. L65 & L68.  Superscript formatting was lost in the exponential numbers.

8. L85-88. This portion of the manuscript requires a bit more exposition.  Unless the filtering is strongly non-linear, it should not matter where it is done filtered regionally and then summed, or summed and then filtered.

9. L89-99. Is the uncertainty of the IEEE coefficient included in the overall estimate?  If not, please justify why that can be neglected.  If it is, please describe that portion of the estimate.

10. L95. Generally phrases like "Note that" or "Is is notable that" are superfluous and can be deleted.  If it's not noteworthy, why put it in a manuscript?

11. L116-118. Hasn't the geodetic series been filtered with a 3-year low-pass, so really the comparisons are only for signals with periods of about 3 years or greater?

12. L121-123.  Please mention here that the CERES EBAF product mean EEI has been anchored with in situ estimate (including an ocean estimate that relies primarily on Argo data).

13. L149. Generally sentences like "Figure x shows" are poor topic sentences, and duplicate figure caption.  How about "Temporal variations of EEI derived from ....agree fairly well with those obtained from the GCOS yearly ensemble and CERES measurements (Figure 3)."

14. L150-161. Loeb et al. (2021) showed a pretty good agreement between an in situ estimate and CERES both for the acceleration of EEI, and the interannual correlation. Their correlation at 1-year resolution is comparable to those here at 3-year resolution.

15. Figure 3 and discussion. It would probably be more interesting to the reader to compare trends over the portion of the record common to all three time-periods.

Marti et al. provide an update on the global ocean heat content change since 1993 based on a geodetic approach. The new time series shows a positive trend of OHC-based EEI, suggesting an acceleration of global heating. This geodetic-approach-based estimate shows a reasonably good agreement with other in situ observations. The paper is good and well-written, and the geodetic approach provides a promising method to estimate OHC and EEI, which should appear in the state of the ocean report. I have several comments on a couple of things and hope to improve this paper:

• Abstract: a trend of 0.75 Wm-2 does not suggest an acceleration of ocean warming, instead, it is “ocean warming”. The number you derived later: 0.29 [0.04;0.56] W m-2 decade-1 for LEGOS-Magellium over 1993-2022 is the “acceleration”. please rewrite the abstract.
• Abstract: The last sentence “This study highlights the importance of rigorously estimating uncertainties based on space geodetic data to robustly assess EEI changes.”. This seems not a key point of this study. The uncertainty quantification is always referring to other papers and not thoroughly introduced in this paper. I would say something to highlight the importance of a combination of multiple lines of evidence to depict ocean warming and its acceleration, because clearly, the geodetic approach shows the value and could be a nice addition to the traditional approaches.
• Introduction, page-1, line 20-24: please give a balanced and more inclusive citation for each group of methods.
• Page-2, line 48-50: this paragraph seems out of place, I suggest putting it after page-3, line 74, i.e. the derivation of GOHC should come after the regional OHC is derived. And, another thing is: please also clarify how you make regional patterns before GRACE (you used the individual contributions to manometric sea level from Greenland, Antarctica, mountain glaciers and from terrestrial water storage before 2002, are you using regional fingerprints or just global time series?)
• Page-2, line 51: Is the salinity effect only neglected in GOHC calculation, not for regional OHC calculation?
• Page-3, line 85-86: I don’t understand why performing the filter step at regional scales is low on GOHC estimate but more on the EEI estimate. What does exactly this mean? Isn’t EEI is simply derived from GOHC according to Eq.(1)?
• Page-4, line 100-119: the presentation and introduction of these datasets are a bit of chaos and not organized: different data products should be better grouped according to the data/methodology difference, so the readers can better understand their differences. Please see Cheng et al. 2022 (https://doi.org/10.1038/s43017-022-00345-1 ) for reference.
• Page-4, line 111-115: Not all five data centers are “Argo centers”. They are fundermentally different from “Argo resulting GOHC change estimates” because ISAS, EN4 and NOAA used all available in situ data, but JAMSTEC and SIO are purely Argo. They should be better grouped and introduced.
• Page-4, line 111-115: all five data products are used in the GCOS estimate, so they are not independent from the GCOS estimate. Please discuss this issue.
• Page-4, line 119-121: I don’t understand this, many of the data products listed above are monthly data (ISAS, EN4, NOAA, JAMSTEC, SIO, CORA, ARMOR-3D), why should you need to interpolate to monthly time series??
• Page-5, line 136: “Over their respective area of data availability”: please clarify which domain you are referring to?
• Page-5, line 146-148: it is not correct: different GOHC estimates used in this study has different ocean-land mask, so their areas are different. And there is no “Argo mask” because different Argo data center also has different masks. Please clarify what is this referring to.
• Page-5, line 149-154: please also discuss the variability in these time series: are the inter-annual variation meaningful (i.e. ENSO) or just noises?
• Table 1: I don’t know what is “Argo mask” you are referring to: mask of which Argo product?