Peer review of: Extinction of eastern Sahul megafauna coincides with sustained environmental (2020)

Reviewers' Comments: 
 
Reviewer #1: 
Remarks to the Author: 
This paper reports results from a truly wonderful new megafauna site in central east Queensland 
Australia. The study certainly greatly expands our knowldedge of megafauna in into tropical Australia. 
I cannot comment on the taxonomy of the remains, so take these at face value. The site has been 
dated with multiple techniques and some environmental context is provided by palynology and the 
identification sporomiela spores in the fluvial sediments that host the remains. I would very much like 
to recommend acceptance of the paper, but I find it is somewhat confused in the message it is trying 
to convey, and some of the paleoclimatic interpretations are dubious at best. I think that has arisen by 
trying to shoehorn the results into the perennial humans versus climate megafaunal extinction debate 
as the high-profile reason for publication. 
 
The argument presented (in a nutshell) is that megafanua lived beyond the timeframe of ‘extinction’ 
suggested elsewhere, and that in the absence of evidence for human presence in the region, the 
assertion is that climate ‘deterioration’ must be to blame. So to take these in turn. 
 
(i) Megafauna lived beyond the ‘42ka’ extinction window: first, the central estimate for the extinction 
window is 42ka, but the error (25th and 75th percentiles) is 37-48 ka. The authors seem to favour, 
from amongst their ages an estimate of around 40 ka for the bulk of the ‘extinction’ at their site. I 
would also note that they have discarded three radiocarbon dates on charcoal (one on a single 
fragment) all of which have calibrated ages of 42-49ka. These are discarded because charcoal in river 
sediments might be ‘a few thousand years’ too old. This is true– a few thousand, but the dates are 
therefore likely to be older than say 40ka (and these are not shown on the figure in the text). The 
large number of OSL dates on the sediment (which are reduced to one bar on the figure in the text) 
are all >38±2.5 ka and up to 66ka, so broadly similar to the radiocarbon, suggesting a minimum age 
of say ~40ka, or within the bounds proposed for ‘extinction’ by Saltre et al.. In contrast, the ages 
least likely to be correct given the open nature of the site are the U-series and maybe ESR dates, 
which do suggest a younger age (ESR not terribly useful either way), all of which are plotted on the 
figure in the text. So, the parsimonious interpretation to my mind would be that the small number of 
U-series and ESR dates are wrong and the large number of OSL (and charcoal) dates places the site at 
or before 40ka, so not hugely different from the existing suggestion, without placing much credence 
on the veracity of the claim that any megafauna lingered on much longer at the site. I guess 
incorporating this into the Signor Lipps modelling of Saltre et al. would presumably reduce the 
modelled central age a little but not much. The authors say ‘Considering the Signor-Lipps effect we 
conclude that the megafauna at SWC suffered local extinction sometime after 40.5±1.6 ka’. I would 
say yes, but probably not long after, with no obvious climate driver for extinction at this time. 
 
(ii) The authors claim the absence of evidence for human occupation of the catchment is evidence for 
a lack of human involvement in extinction. You don’t have to go too far northwest of the site to find 
Gledswood Cave with occupation dated to (I think) 38ka, and given the paucity of sites in general for 
human occupation, it can be reasonably assumed that humans were present in the catchment. 
(iii) The authors claim ‘climate deterioration’ ‘intensified’ after 40 ka and point to a number of 
compilation studies that suggest this (some do, some don’t). It is true that the one study within the 
catchment (Croke et al., 2011), based on OSL dating of river terrace sediments has a gap in dates in 
the 5,000 year bin centred on 35ka that might indicate drying at this time, but there is a much larger 
gap in OSL ages between 65 and 75ka, coincident with a stage 4 that has been recently described as 
‘glacial’, with very low sea levels and ‘dustier’ (De Deckker et al., Quaternary Science Reviews 204 
(2019) 187-207), and megafauna did not go extinct at that time a mere 20ka earlier, despite harsher 
conditions. The evidence from vegetation is equivocal at best and the explanation actually a little 

tortured in places. The authors claim (Line 219) ‘Vegetation records from ODP820 indicate regional 
reduction in grasslands (sclerophyll herbs) from ~50 ka reaching 220 their lowest levels at ~35 ka’. 
Wouldn’t low grass pollen in ODP-820 coupled with tree expansion, ordinarily be interpreted as a likely 
a wetting trend through the interval to 35ka – consistent with the pollen evidence from the site itself, 
which suggests abundant tree species (eucalypts, casuarina, melaleuca) - and very little grass . This 
does not suggest a very dry climate at least at the time of sediment accumulation, nor well into the 
period of ‘climate deterioration’ that is claimed. Fire will be present at all times given the extensive 
savannas and the meaning of the charcoal signal in ODP-820 I think is currently difficult to discern, as 
elsewhere. 
 
So – in summary – a great data set, great site, but I think the interpretation needs a serious rethink. I 
personally don’t care whether extinction was by humans, climate or a combination, but it has to be 
argued on the evidence, not by tossing out the bits that don’t fit. 
 
Other things: 
L253 - The authors make the statement in the text: ‘Sporormiella is present in low numbers at SW9 
(Supplementary Figure 34 and Supplementary Table 
24) leaving its relationship with the diverse herbivorous megafauna equivocal’. The data are not on 
Figure S34, but in the table, SW9 has 59 grains per cm3, and other samples up to 80. These are high 
levels compared to amounts reported from lake and marine sediments, and I think bolster the 
argument that Sporormiella is associated with megafauna. 
 
Supplementary table 20 – S-ANU 40224 – units not correct as are given in pMC, not F 
 
 
 
Reviewer #2: 
Remarks to the Author: 
The authors describe the late Pleistocene fossil assemblage of South Walker Creek, northeastern 
Australia, which preserves at least thirteen extinct and three extant species of megafauna comprising 
aquatic and terrestrial reptiles and marsupials, including several possible previously un-described 
species. Dating shows local extinction after 40 ka, coinciding with the onset of climatic and 
environmental change. 
 
Megafaunal species diversity at 40 ka from South Walker Creek is greater than that of southern 
regions of similar age, which is contrary to expectations if extinctions followed postulated north to 
south coastal human migration routes. Therefore, the authors argue the results do not support rapid 
or synchronous human-mediated continental-wide extinction. Instead they argue the extinctions 
coincide with regional aridity. 
 
These arguments in this context are original and supported by the data presented. The notion that 
there is no evidence for humans causing rapid or synchronous extinction of megafauna across the 
continent is of interest to others in the field, and will promote further debate. 
 
Matt Cupper 
 
 
 
Reviewer #3: 
Remarks to the Author: 
In this manuscript the authors claim to demonstrate that the extinction of megafauna in eastern Sahul 

is consistent with environmental change postdating human occupation by a minimum of 10,000 yrs. 
Overall I think that this is argument is well-supported by the evidence they present and there can be 
no question that this represents a finding of broad interest and significance. 
 
Line 56 and elsewhere: this reviewer is in complete agreement with the proposition that there are 
“few reliably-dated Upper Pleistocene sites” in Sahul. However, and may be I’ve missed it, I do think 
that this a point that requires elaboration. What constitutes a reliably-dated site? On line 172 the 
authors note that they used direct dating and multiple dating techniques to constrain the age of the 
fossils they have dated. This seems solid to me, but the definition will likely always be an arbitrary one 
that in itself has long been hotly debated and see Meltzer & Mead (1985). For example, Roberts et al. 
2001 claimed that only sites with articulated remains could be considered as reliably-dated. This 
determination has been criticized by others, e.g., see Wroe et al. 2004, and has not been widely 
accepted or used by others. Regardless, I think that the authors should provide a more explicit 
definition, not only for what they consider to be reliably-dated in the context of their own work, but 
what they accept as reliably-dated by others. 
 
Line 189: “Considering the Signor-Lipps effect…” I’m really not sure if this effect can be determined on 
the basis of so few reliably-dated sites, but if it can, how have exactly have they accounted for this? 
 
Lines 243-244: Deterioration in climate and vegetation “would have significantly impacted terrestrial 
megafauna survival, especially the herbivores and more specifically the grazers”. I suggest that 
anything significantly impacting herbivores must have the impacted carnivores that preyed on them. 
In fact, we would expect the carnivores to go extinct first as herbivore densities fell below densities 
that could sustain them. 
 
Line 258: “limited evidence of interaction exists”, i.e., between humans and extinct megafauna. To the 
best of my knowledge there is no unambiguous evidence supporting this contention and certainly no 
kill sites. 
 
Line 280: “contrary to what would expected” I think should be “contrary to that which would be 
expected”, although the editor will be the judge on this. 
 
I think it would be appropriate to have a brief concluding sentence… 
 
Roberts et al. (2001) New Ages for the last Australian megafauna, Science 292, 1888 
Wroe et al. (2004) Megafaunal extinction in the late Quaternary and the global overkill hypothesis, 
Alcheringa 28, 291 
Meltzer & Mead (1985) Dating Late Pleistocene extinctions in “The Cambridge Encyclopedia of Human 
Evolution, 369-371 
 
 
 
Reviewer #4: 
Remarks to the Author: 
 
This is an interesting and important paper reporting site/s from Eastern Australia that document a 
range of megafauna and 'late' survival, while canvassing possible extinction scenarios and timing. I 
think this is significant for adding to our knowledge of megafauna and their various contexts across 
Australia (and Sahul). 
 
The paper is well written in places but I find that some of the detail is not clear and some of the 

writing is also not clear. The discussion of sites which may have a human association is missing and 
when mentioned the authors don’t appear to be familiar with the data. I think that the authors need to 
make the whole presentation accessible for a general audience, which at this stage is not. 
 
I note there are no images of the site or material in situ which would have helped get a feel for the 
location and context. 
 
I have a number of other comments to make and list them in dot point form below. 
 
• Firstly, referring to the ‘Upper’ Pleistocene is a little confusing. I know name changes have occurred 
and more generally it has been commonly referred to as the Late Pleistocene C.126ka +, though this 
paper also includes discussion of Middle Pleistocene as well. (Middle Pleistocene c.781 ka to 126ka). 
Because of the mix-up with names it is a little confusing. If the authors wish to use the term ’Upper 
Pleistocene’, then I suggest they define it up front (in the title). It just needs clarification. 
 
• Line 48 – the authors must acknowledge that the 40-44kg cut-off for megafauna is a little 
misleading. There were a range of animals <40-44kg that also went extinct, and were larger than 
modern day correlates. It was not just confined to larger species. 
 
• Lines 57-58 –I have a real issue with referring to, even if indirectly, an extinction window, initially 
proposed by Roberts in the 2001 Science paper. This paper is very flawed and has been shown to be 
statistically invalid. The 7 sites used in the analysis to determine the ‘extinction window’ were mostly 
not described in the literature (so where did the samples come from for the dating study, we still don’t 
know). This was pulled apart by Field and colleagues in numerous publications, at least one of those 
should be cited here as a counter to the Roberts etc assertions, e.g citation 47. 
 
• Line 75 – have these dates been published previously? Isn’t this what the paper is about? 
 
• Line 88 – I would prefer to see some description of the site and its setting to be able to understand 
its context before launching into this description 
 
• Line 89 ‘Rich deposits of body and trace fossils’???? What does that actually mean? 
 
• Line 90 recovered from where? 
 
• Lines 109-112 I find this a rather ‘double negative’ convoluted explanation that has no real 
relevance to this discussion. How can we assess the likely taphonomic factors if we don’t even know 
what the site context is? And why are we talking about species that are not there. Surely the few 
examples listed above illustrate this point? 
 
• Lines 114-116 – I still don’t get why the authors talk about a ‘possible new species’, it is or it isn’t. 
Perhaps a more conservative description would suffice. 
 
• Line 117 – don’t you mean comparison with….postcranial dimensions? 
 
• Line 88-134. I find this section interesting but overly long and convoluted. The one sentence that 
comprises a paragraph (Lines 125-127) would be much better higher up the section. 
 
• Line 137- this is the first time that four sites are mentioned. This is why we need some context 
higher up the paper. It assumes knowledge of a whole range of information that hasn’t been 
presented yet. 

 
• Line 140 main channel deposits? Is this a fluvial deposit?? Is there a reason why the authors think 
this is in situ? What do they actually mean by ‘articulated’, surely something of this age would have all 
connective tissue absent, do you mean ‘anatomical order’? 
 
• Line 164-171 – Again we are dealing with assumed knowledge with no indication how this relates to 
context. I find this very frustrating. 
 
• Line 173 – As much as we would like to be able to directly date fossils this is not always possible. U-
series and ESR methods as relative dating methods are useful, but only when considered in concert 
with absolute techniques such as C14, which I note that the authors have tried to do. However, it 
would be considerably stronger if they could clearly demonstrate the whole picture here. I know I keep 
reiterating this but the context is as important to assess any assemblage – are we to assume 
otherwise? 
 
• Line 235 – I would suggest that the detailed work of Mooney et al is not just a ‘debate’. It looks at a 
range of records to support their argument. I also note that the Moss paper cited is an analysis of the 
ODP820 core, so offshore and conflated. What does the archaeology tell you from this area? I am sure 
would be hard pressed to place humans here before 40ka on current records, let alone at population 
levels that would have such effects recorded. To have such a major impact may relate more to 
changed climatic patterns etc, as stated in the next sentence. 
 
• Line 238 – an interesting observation, if in fact there were enough megafauna around that their loss 
precipitated such events. We have so little data on this it would be hard to say what population levels 
actually were, which is clearly important to this scenario. 
• Line 257-259 Citation choice a bit odd I would note that the Hamm et al paper has one element of 
megafauna and not in the cultural levels – what does that mean? It is clear that there is little to no 
evidence for any interaction of humans and megafauna. The only two sites that may contribute to this 
are not mentioned here – Nombe Rockshelter and Cuddie Springs. Hardly a comment on a human 
involvement. 
 
 
• Line 262-263 – I think you need to mention humans here. Certainly, people don’t necessarily 
‘occupy’ that space. A ‘human presence’ is what you mean, so say that. 
 
• Line 266+ - you have absolutely no evidence of people in this area at this time, the way the authors 
talk about this implies there is a coexistence. If you look at the fossil record across Sahul there is 
clearly so little evidence of a human association that it hardly bears commenting on other than to say 
there is NO evidence of a human association. 
 
• Line 283 – this is selective citation at best. The authors would be better citing the most recent Allen 
and O’Connell paper, or even going back to the original sources the book called ‘Sunda and Sahul’ – 
Birdsell, Horton etc. We really don’t know which way people entered Sahul. Looks like multiple 
migrations and from multiple directions, the north coast of New Guinea being the easiest. With 
Madjedbebe predating most of the sites on Sahul by a significant period it cannot be relied upon as 
the only marker. The authors are trying to cover this but need to rethink this a little. 
 
• Line 272+ I would be a little more circumspect about this. 
 
• Line 283-287 – it needs to be considered on a continental scale and in a global context. Extinctions 
were occurring across Sahul, at different rates and times and it would be best to make that point. 

 
• Line 711 – it must be made clear that this is covering this part of the extinction spectrum. There 
may have been earlier events – as suggested by the Wroe et al 2013 paper? 
 
• Line 735 – don’t you mean Sahul? And if so why haven’t you included Nombe. Yes it dates to MIS 2 
but surely that is very important. At least in the discussion. Denham and Mountain recently published 
a new dating study that confirms the original reports and places the megafauna well within the human 
time-frame. Sutton et al 2010 reviewed fauna from New Guinea. 
 
• Line 743-"the age of units SU6A+B at have been debated due to potential sediment mixing and 
reworking. We have used US-ESR dates taken directly from fauna to represent the age of these units." 
 
I find this an interesting comment. Perhaps the authors need to read the various papers written by the 
site investigators (not the ESR dating experts) that clearly describe the deposits, the fauna and their 
context, and in all cases defend the site against the unsupported assertions of the Roberts/Grun 
collective. The Grun et al paper may have been the last published on dates, but I note that 
subsequent papers have challenged their conclusions. Perhaps you should read them? Have you talked 
to the site investigators? Does the ESR sequence trump C14 and OSL? I don't think so. This is not 
good scholarship. 
 
• A general comment. This paper has potential, but needs tidying up. More information up front is 
needed to understand the context before launching into the descriptions. The MNIs reported here are 
very low, but the impression I get is there was a significant deposits? Also, I would like to see the 
various age populations reported for the single grain OSL analysis, rather than/or in addition to the 
weighted average mean. I also note that there is one combined pollen sample because of the few 
pollen grains surviving in the samples. This should also be explicit. It actually just reports a point in 
time, especially considering the broad time span and deteriorating conditions that must have prevailed 
in MIS3. The area covered in this study covers about a third of the Australian continent and probably a 
couple of environmental zones. It would be useful to understand that. The Sporormiella. What is the 
take home message from that, other than it is ‘there’. As we know that many modern extant fauna 
dung also harbours these spores, I am not sure what its presence there tell us. Maybe I missed it, but 
how do the authors see these deposits forming? I don’t remember seeing a section on site formation.