The Detection and Attribution of Northern Hemisphere Land Surface Warming (1850–2018) in Terms of Human and Natural Factors: Challenges of Inadequate Data

Round 1

Reviewer 1 Report

The present paper by W. Soon et al. represents a most relevant,
interesting, and timely contribution to the ongoing debate
about the relative impacts of solar and anthropogenic factors
on the observed temperature increase since the middle of the
19th century. Assessing two different temperature time series ("rural
and urban" and "rural only") as dependent variable, and two
differently varying Total Solar Irradiance (TSI) time series,
plus one combined anthropogenic and one volcanic driver,
as independent variables in a multiple linear regression analysis,
the authors arrive at quite different conclusions as to the primary
driver of the observed warming.

The paper is clearly written, the lines of argument can be followed
easily, and the controversial literature on the topic is thoroughly
payed tribute to. Apart from some very minor issues (see further below),
I'm therefore inclined to recommend immediate publication of the paper.

That said, I would like to express some concerns regarding the choices
of the independent and dependent variables, some details of the
regression analysis, and the utilized evaluation metrics. All my
comments should be understood as a kind invitation to reconsider some
aspects of the work and to add, at places, a few appropriate comments
and perhaps some more results which might be helpful for further
discussions. Yet, I do not insist on any specific changes, and I
could also live with the present version if the authors prefer to
keep the paper as it is.

1) Dependent variable: I perfectly understand the motivation to
evaluate  - in addition to the "rural and urban" data which are thought
to be biased by the urban heat island (UHI) effect - also the "rural
only" data. However, given the extreme reduction of the remaining
station count for the latter (something in the order 10 before 1890,
see Fig. 1d), I have the nagging feeling that the authors might have
replaced one evil (UHI bias) by another (very poor statistics). In this
respect, even the claimed decrease from the 0.89°C/century to
0.55°C/century warming seems not without problems. While the authors
admit the strong noisiness (Fig. 1c) resulting from the reduction of
the stations' number, they still use the extreme outlier at 1867 for
the definition of one of their evaluation metrics (page 16, line 719,
and Supplementary material), which I consider as hardly justified. In
future work, one might think about constructing an optimum combination
of the data of Fig. 1a (with their likely UHI issues in the later part,
including the suspiciously shallow decline between 1940 and 1970)
with those of Fig. 1b (impaired by the poor statistics in its early
part). Such a combined series could then also be cross-checked with
SST data (although the provocative question comes to mind: why not using
SST data in the first place?). While all this would clearly go beyond
the scope of the present paper, at least some more remarks seem
appropriate.

2) Independent variables

2a) Following Connolly et al. 2021, the authors consider two types of TSI
data, the low-variance (updated) Matthes 2017 data and the high-variance
(updated) Hoyt and Schatten 1993 data, a choice with grave consequences
for the relative weights of solar and anthropogenic factors resulting
from the multiple regression. In this hardly decidable situation it
might be worthwhile to compare their results with those that rely on
the (in contrast to TSI!) uniquely defined geomagnetic aa-index (Stefani
2021). Given that the very TSI is certainly not the only effect of
solar activity on climate (as recently evidenced by Scafetta 2023 who
found an "amplification factor" between 4 and 7), there is no reason at
all to prioritize TSI over aa. As for an appropriate evaluation metric,
see below.

2b) While less problematic, also the use of the second independent
variable "all anthropogenic forcings combined" from the IPCC Annex II
dataset is not without caveats. Herein, there are some features, e.g.
the slight decline between 1945 and 1965, that is not present in the
CO2 data but results only from the aerosol forcing (Fig. S2i), which
in my opinion should be considered as a sort of "fudge factor". Later,
I'll come back to the problem that the use of this mixed data-set
hampers the derivation of a climate sensitivity.

3) Regression: First, I applaud the authors for having enhanced the
sequential regression analysis as carried out in Connolly et al. 2021
by a more appropriate multiple regression analysis (also reacting
on the criticism by Richardson and Benestad 2022 related to the
error-proneness of sequential regression analyses when applied to
co-varying independent data). Yet, somewhat related to the discussion
under 1), I'm a bit concerned about the use of an "unweighted least
square", given the dramatically changing statistics due to the steep
drop of the station number before 1890. In the discussion of the
results of Richardson and Benestad 2022 (pages 21/22) the authors
attribute the substantial underestimation of the solar contribution
exactly to the use of a "weighted last square" method. Honestly,
since a "weighted last square" seems - in view of the drastically
changing station count - quite reasonable to me, I would feel a bit
nervous about this difference!

4) Evaluation metrics: While I have nothing against the utilized
evaluation metrics (except the one in the Supplementary Material
which assigns a special role to the exceptionally low value of the
noisy(!) "rural only" data at 1867), I'm a bit surprised that the
authors have not tried to derive what most people would consider
as most important, viz., some sort of climate sensitivity (ECS or
TCR). In principle, this is something which should easily be
inferable from the relative weights resulting from the regression
(it's certainly hidden somewhere in the accompanying Excel files,
though I have not checked it). Admittedly, the use of IPCC's
"all anthropogenic forcings combined" represents a certain obstacle
for that inference, but given that it is dominated by CO2 (plus
some minor aerosol part), it should not be too complicated to do the math.
Such a derivation of a climate sensitivity would be all the more
important as recently the two different multiple regressions by Stefani
2021 and Scafetta 2023 had arrived exactly at the same range of
0.6-1.6°C/(2xCO2), when using SST data as dependent variable, and
a high-variance TSI in Scafetta's case (this interesting correspondence
could perhaps by highlighted in subsection 3.3). A comparison of those results with the results obtained in the present paper would be very valuable. Quite similarly, the second weight factor resulting from the
regression should give some "amplification factor" for the
TSI (which had been shown in Scafetta 2023 to lay somewhere between
4 and 7). Actually, if the authors are willing to add just some material
to the paper, this would be the most important one.

Minor remarks:

- Page 1, line 28: I think the affiliation is "Lomonosov Moscow State
University" (without comma)

- Page 3, line 138, the citation [11] should be added behind Matthes
et al. (2017)

- Page 5, line 260: In my view, this reaction to the substantial
criticism of using sequential regressions for co-varying independent
data by Richards and Benestad (2022) sounds a bit evasive. Perhaps
one could be a bit more honest here and replace "proposed" by "showed"
or "corroborated" or something similar...?

- Page 7, lines 338-340: While there are certainly many good reasons
one might criticize AR6 for, its authors should not be made responsible
for not reflecting findings that appeared after the deadline for
consideration.

- Page 7, line 367: compilation -> compilations

- Page 15, line 668: factor of five: I think Scafetta 2023 found factors
of 4-7 (his page 16)

- Page 16, line 821: % -> percentage

- Page 21, line 880: atttribution -> attribution

- Page 24, lines 1068-1073: I'm not sure whether the citation of
Mann et al. (2021) is really appropriate. At least, one should make
a comment relating the very minor contribution of volcanic activity
for the decadal/centennial variability as found here to the ideas of
that paper.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 2 Report

General comments:
The submitted manuscript makes an important contribution to two major
problems: (1) The difference between the urban + rural, and rural only
temperature time series, and (2) use of two different solar irradiation records.
These are important questions that should be published.
However, the manuscript has, according to my opinion, very poor structure. Too much time and space is devoted to the criticism of the IPCC including several long direct quotes. Criticism of the IPCC should not be the main objective of the paper. This should be reduced to a paragraph. Similarly a detailed description of what
as been published in the C2021 distracts from the new work presented and
should be reduced to a citation and a few lines.
In general, the authors are using too many words and they are describing topics of
peripheral interest which detract from the main goal. If you can say something in
one paragraph, do not write two.

Consequently I recommend a major mandatory revision.

On a technical side I am not convinced that regression analysis over the whole
1850-2020 time-span is the best way to treat the problems. Since there are timespans
with increasing and decreasing temperature, I am not sure what is the
meaning of linear trend for the whole 1850-2020 period. I would suggest to
consider some time-interval separately, especially the post 1970 time-interval.
Just a few specific comments:
In general there are many different ways how to proceed with a regression
analysis. As long as the method used is described different approaches are
acceptable.
Fig. 1: The differences between rural and urban and rural only would be more
visible if the two time-series would be plotted on the same graph.
Comparing the linear trends for 1850-2020 years is not very useful, since the
direction of temperature change changes few times within this time span. The
total interval can be divided into several segment and compare the trends in each
separate segment. The last segment may be approximately 1970-2020.
Fig. 2: You use the same color for many different records. Nobody can see the
differences. Is this the purpose of the figure?
Fig. 4 and 5: The data would be easier to understand if some of the rural+urban
and rural only results would be presented in the same figure. Similarly with two
different TSI cases

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Round 2

Reviewer 2 Report

I still feel that the attention devoted to IPCC and to C takes still too much space. Please, reconsider, if you can reduce this. This is my last comment; after that I leave it up to the authors.

Author Response

Reviewer 2: “I still feel that the attention devoted to IPCC and to C takes still too much space. Please, reconsider, if you can reduce this. This is my last comment; after that I leave it up to the authors.”

---

We have now deleted the old Section 1.1 that summarized C2021. We have also tightened up the text in the old Section 1.4 (now 1.3), removing some of the discussion of the IPCC and also some repetition. This has substantially shortened the introduction section from 3399 words to 2635 words.

We hope you agree that this revised manuscript is now ready for publication.