Really excited about this new paper extending the temperature record further back in time. One small recommendation for the authors is to show how their pre-1850 land temperature reconstruction compares to that published by Berkeley Earth (which also goes back to the 1700s).

I'm rather bothered by the use of "Taylor et al. (in prep.)" to describe the LEK process of estimating normals and how little information is provided to describe the process in the current manuscript.  The LEK approach is one of several core innovations being used in this manuscript, but there isn't enough detail appearing in the text to really understand what is being done.  Or more precisely, I could imagine several different ways to formulate such a Kriging process, and the current text is much too vague to be clear what approach is being taken.  For example, how are the covariances being estimated?  Is there explicit consideration of common covariates (e.g. latitude, elevation)?  Further, a single sentence is used to describe a test of the accuracy of the method (again referenced to Taylor et al.) but without enough elaboration to be clear exactly how it is being tested.  Nor does it say whether the error depends on how much of the 1961-1990 interval is missing?  Is the error different depending on the time coverage of the station (e.g. is a station running 1980-2020 going to have more accurate normals than one running 1880-1920?)  Based on personal experience with station biases and Inhomogeneities, it feels implausible that the typical error in estimating normals via the process described would only be 0.2 C when considering station time series that end well before the modern period.

Given that LEK is one of several core innovations being applied here, I would suggest that either it needs to be thoroughly described in this manuscript (perhaps in supplementary methods?) or this manuscript should pause publication under after "Taylor et al. (in prep.)" can be published and made available.

The maps summarizing two decades at a time are helpful, but it is still hard to get a sense of how much (or how little) data is available.  I would urge the authors to also include a time series of the number of observations available over time, and the number of non-empty grid cells over time.  This could be done separately for global, land, and ocean.  I believe such plots would be very helpful in getting a sense of how much data is being used when, especially for the early parts of the record.

Strangely, this paper fails to acknowledge that there are in fact two kinds of diurnal variability affecting marine air temperatures.

The paper heavily discusses diurnal heating biases arising from the ship absorbing solar radiation and warming during the day.  The authors are right to pay careful attention to such heating biases since the warming of the ship can often spuriously raise the daytime marine air temperature measured by the ship by ~1-4 °C (e.g. Cropper et al. 2023) relative to the corresponding nighttime measurements by the same ship.

However, despite this extensive attention to diurnal heating biases, the paper never acknowledges that natural diurnal variability can also exist in marine air temperatures.  In many contexts, the buffering capacity of the oceans often makes diurnal temperature variability of the ocean and air quite small (e.g. ~0.1 °C).  But in the tropics, in shallow water, and/or near shore the diurnal temperature range can be substantially larger (e.g. 0.5 °C).  This is especially true in near-shore environments, where differential heating of land and ocean can lead to predictable intraday shifts of wind direction from off-shore to on-shore with corresponding large variations in the characteristics of the advected air mass.  Though natural diurnal variability is smaller (and sometimes much smaller) than the spurious diurnal heating biases, I don't think it is reasonable for a paper focused so extensively on marine air temperature to entirely ignore the potential for natural diurnal variations.

Natural diurnal variability, to the extent that it exists, isn't a bias in the sense that the term is normal used, rather it is legitimate feature of the weather.  The discussion in the paper is sometimes confusing or even misleading because it fails to separately address the existence and possible impacts of such variability.

Most measurements of diurnal temperature range over the ocean have focused on the variation in ocean temperatures, e.g.

HadDTR (https://www.metoffice.gov.uk/hadobs/haddtr/)

AMSR-E Satellite measurements (Large & Caron: https://doi.org/10.1002/2014JC010691)

Such natural diurnal temperature variations vary not only by location, but also by time of year.

The diurnal variation in marine air temperatures will often be at least as large as the corresponding variation in sea surface temperatures, and in near-shore environments, the diurnal range of marine air temperature can be considerably larger due to regular patterns of advection from terrestrial air masses.

The corrections applied for diurnal heating biases (Cropper et al. going back to BKT) are primarily designed to deal with the biases arising from the ship itself.  For example, despite natural diurnal variability exhibiting substantial spatial structure, the positional dependence of the corrections appears to be limited to considering latitude and solar declination.  Nonetheless, since the bias adjustments are being empirically fit, the corrections may partially capture (and hence remove) natural diurnal variability in addition to the ship-based diurnal heating biases.  However, it is unclear from the present paper and Cropper et al. to what extent that is the case.  Based on the present methods, one might suspect that ships that travel across regions with varying degrees of natural diurnal variability will have poorer fits.  The authors say "... the full diurnal cycle is removed from the data and GloSATMAT should be considered a nighttime-equivalent dataset", but that's only true to the extent that the Cropper et al. process removes both the ship-based diurnal heating biases (that it was designed for) and the marine air temperature's natural diurnal variability (which it was apparently not designed for).

To the extent that natural diurnal variability persists in the bias-corrected marine air temperatures, then changes in the time-of-day composition of the measurement network could lead to biases in the apparent marine air temperature trends.  In this context, it might be useful if the authors would provide time series indicating what fraction of the marine air temperatures are nighttime vs. adjusted daytime measurements.

In terms of revisions, I'd like to see the authors acknowledge the existence of natural diurnal variability in marine air temperatures and discuss the extent to which the Cropper et al. process is capturing the natural variability in addition to the ship-based heating biases.  Further, I would hope for some discussion of the potential impact that residual natural diurnal variability might have on the assessment of long-term marine air temperature trends.

Great to see this important contribution to integrations of early instrumental temperatures. Just briefly with regards to the Hausfather/Rohde comments and Referee #3:

It seems unlikely that the very large variance increase in GloSAT (and BE) prior to ca. 1860 is just caused by the volcanic activity, as it persists also before and after the large eruptions. In PAGES2k (2019) there is a comparison to an early instrumental composite over 1775-1900 (their Figure S19), which shows comparable variance with the reconstructions over this time period and no such substantial variance changes. Even though this composite is only from Europe, this may add to the argument that the pre-1860 variance inflation may be an artifact of replication/coverage changes.

Nevertheless it is likely that the variance of the PAGES2k ensemble median is too small (as already stated in the paper), mainly due to the averaging accross the large ensemble. This could be assessed by a member-by-member comparison for both ensemlbes for Fig. 5, although this is already partly addresseed in Fig S5. Given the probable under- and over- estimation of variance by the two curves, it seems likely that the truth is somewhere in between...