Review Reports

Round 1

Reviewer 1 Report

See attchment.

Comments for author File: Comments.pdf

Author Response

Please check the attached file.

Author Response File: Author Response.pdf

Reviewer 2 Report

In the present article the authors claim is to be able to detect offshore Stone Age sites located at the seafoor or embedded in the seafloor sediments through application of a chirp subbottom profiler. In particular, they claim to be able to distinguish between anthropogenically knapped and naturally cracked lithics through acoustic (seismic reflection) measurements.

For proving their claims the authors present seismic example records showing acoustic amplitude anomalies of different intensity in the water column. In the figures strong amplitude anomalies occur above artificially knapped flint stones packets independently of whether they are placed on or underneath the sea floor. In contrast, the acoustic images do not show amplitude anomalies in the water column above packages of naturally cracked lithics. The different sorts of flint had been placed at or dug into the seafloor by the authors.

The authors attribute the amplitude anomalies to acoustic resonances that they assume to be generated only by anthropogenically knapped flint stones and not by naturally cracked flint stones. To support their hypothesis the authors report of a number of sound experiments of flint rocks previously performed in labs.

Having a tool for detecting offshore Stone Age sites is, of course, a dream of many archaeologists. But the authors fail to prove that this dream became reality. It is the following points that bring me to conclude that the whole story is either a product of “wishful thinking” or even “fake”:

1. In the seismic sections the acoustic anomalies, which are claimed to be indicative for anthropogenic flint, plot in the water column well above the seafloor where the flint samples had been placed. The vertical scale in the acoustic “depth” sections is actually reflection travel time. Therefore: if these signals in the water column were indeed caused by the flints at the sea bottom, the signals would be pre-causal because they arrived at the acoustic receiver before they were created at the sea bottom. This contradicts common physical understanding.
2. There are many possible reasons for acoustic amplitude anomalies plotting in the water column, including fish swarms, gas bubbles, too short recording windows allowing multiple reflections from previous shots to interfere with follow-up shots, plotting and processing artefacts, and noise from different sources (processing artefacts, instrumental failure, incorrect operation). All of these should be properly excluded before strange mechanisms might be taken into consideration for an explanation. However, the authors do not describe the applied instrumentation, recording parameters and processing steps in a scientifically sound and sufficient way.
3. The same applies to the description of the lab experiments and their results. It is not even clear if the sound experiments were conducted on flint rocks on air, under water or buried in sediments under water (only the latter would be relevant).
4. There is no assessment of the spatial resolution of the seismic measurements.
5. There is no proper description and critical discussion of the onsite under water experiments (geometry, rock packings, acoustic properties of the materials and so on).

I do not see a way to improve these shortcomings in the frame of a revision. Therefore, I recommend rejection of the manuscript.

Author Response

Please check the attached file.

Author Response File: Author Response.pdf

Reviewer 3 Report

Your paper has been an absolute pleasure to read. I consider myself a very careful reviewer, but I really cannot find any significant flaws in your paper. Yes, a few sentences seemed a little lacking stylistically, and to achieve perfection, you might want to have someone from outside the team of authors take another look at it. But it might as well be published just as-is; and that is also what I will recommend to the publishers.

Your contribution is, at the same time, an exciting expose of a technology with phenomenal potential and a wonderful survey of submerged sites. It clearly represents a very well-coordinated team effort. Congratulations on your achievement.

Author Response

Please check the attached file.

Author Response File: Author Response.pdf

Reviewer 4 Report

This is an interesting development work focusing on the detection of submerged Stone Age sites exposed on the sea-/lakebed or covered by sediments remotely, which, if successful, would enhance our knowledge about this hidden heritage considerably. I had high hopes for this manuscript (based on its abstract) and wished to find new solid results from the testing sites across Europe, the US and Near East. Nevertheless, I am sorry to say that I am disappointed, because the manuscript presents still an early development stage of the HALD (Human-Altered Lithic Detection) approach, which has been developed and its previous results published for quite some time already. In addition, quite extensive parts of the contents of this manuscript have already been published (including some of its figures and their captions) and, therefore, the authors could have concentrated solely on their new testing and observations instead of repeating already available data.

The authors state that the approach has already been successfully tested at several submerged sites, but, in fact, the actual verification via ground-truthing (by way of underwater survey, excavation or coring) of the ‘haystack’-shaped anomalies confirming the viability of this method has until now been reached at very few sites (in the US) and in the form of surface finds. It is also mentioned that the approach would work with even single pieces of knapped flint and with finds buried inside sediment (in optimal recording conditions), even though the remaining ‘verified’ sites represent more or less preliminary assumptions reflected against the previously recorded fieldwork observations made years or even several decades ago with no actual up-to-date ground-truthing data via excavations or corings. Of course, already published work does not count in this review, but I still cannot find enough hard evidence confirming the viability and applicability of the HALD approach at its present state and more research, especially in the verification part, is needed.

Introduction is very broad and the relevant topics associated with this manuscript begin practically at row 86 and text before that may be shortened and summarised quite extensively. At the end of intro, it is concluded that the methodological testing is still on going and experiments have still to be performed for verification. This is very true, even though much more positive considerations about the viability of the approach are already stated in various parts of this manuscript. I find this confusing and, therefore, considering this manuscript as a working paper focusing on improved methodology and testing instead of a 'Highlight Article' would be more appropriate. In this way, the previously published parts may be removed, their results only summarised in short and more focus could then be directed to the newer testing and their findings, which would improve the contents and readability of this manuscript considerably.

Materials & methods is basically a theory section describing the background and the acoustic laboratory measurements of flint. Some parts of this section (incl. Figs 2 and 5) have already been published (see references 41, 49-51). The laboratory measurements (by Boumda) of the two flint blades described in detail represent new information and constitute one of the most solid parts of the whole manuscript. The basic information about the case study sites now described in Results section could be moved already here.

Results section describes the testing sites across Europe, the US and Near East (already known sites: Israel, Switzerland and Denmark; hitherto unknown sites: USA, Sweden and Denmark). Strangely, I could not find the Swedish results in the manuscript, even though the testing in Kalmar is mentioned a few times. Parts of this section (incl. figs 9, 10 and their captions) have already been published (see reference 41; I cannot check reference 42, because it is still in press). In general, it is difficult to distinguish novel findings from already published data in this manuscript. With the Atlit Yam site (Israel), it is mentioned that the acoustic anomalies above the previously distinguished cultural deposits covered by up to 2 m of ‘medium-sized sand’ (I wonder what that means?) is supposed to support that knapped lithics may be detected even embedded in sediment - without ground-truthing, though. Similarly, in Denmark, the haystack anomalies were not verified on site, but they were assumed to represent lithics based on previous fieldwork recordings and experiences gained in Israel. The sites in Florida yield more promising (and new) results, however the lithic scatters detected by divers were very abundant surface finds and they were restricted to small areas. Still, this part of the Results section seems promising and the authors could have highlighted this more instead of repeating the already published data. The Roskilde Fjord and Lake Zürich results are again somewhat confusingly presented and the suggested anomalies were not properly ground-truthed. In general, the use of fieldwork information from several decades back as verification may only be seen as indicative, and there may be rather large accuracy problems in matching up the cultural deposits with the acoustic anomalies based on old coordinate recordings and other site observations. Therefore, I would consider most of the ‘verified’ results presented in the manuscript as suggestive. If the authors disagree, I would encourage them to delve more deeply into this issue.

The acoustic testing has concentrated mostly on flint, which is however understandable, because it has constituted the most focal material in producing lithic tools in prehistory. Still, the authors are quite optimistic with the approach’s applicability with the other lithic materials as well, even though their acoustic properties have not yet been explored. This would be an interesting addition to the testing in the future, and quite an essential direction, if the authors wish to explore the general applicability of the approach besides flint. In addition, the geological make-up of the sediment in question and its possible effects on the detection success is still lacking, which I find fundamental in connection to this development work. Lastly, verification of acoustic anomalies via underwater excavations and corings are necessary to be able to step to the next level of development and reveal the full potential and applicability of this approach.

Nevertheless, I would like to thank the authors for their determined and tireless work within the HALD approach and I warmheartedly encourage them to continue.

 

Comments for author File: Comments.pdf

Author Response

Please check the attached file.

Author Response File: Author Response.pdf

Round 2

Reviewer 2 Report

For this review I reread the manuscript carefully and studied some of the cited previous work of the authors in detail, especially articles [51], [52], [53] , in which they outline their laboratory and numeric studies on the acoustic responses of lithics,  and [41] and [54] providing some more information on the field measurements highlighted in the present article. In this regard I also tried to get access to [42], which turned out to be not available publicly though.

The articles show that the authors have seriously attempted to find a foundation for their claim, so I apologize to the authors for having suspected that the presented material might possibly be “fake”.  Still I am convinced that the conclusions the authors are drawing from their lab and numerical experiments and their field measurements are not correct and not backed by their analysis, and that their central statement is wrong. As central statement I consider their claim of being able to distinguish between anthropogenically knapped and naturally cracked lithics through hydroacoustic field measurements. 

I come to this conclusion because the authors do not prove their claim in a convincing way, neither experimentally nor through a sound physical model. Let me explain in more detail why I think this.

The physical model, on which the authors’ build their claim, is the following (if I understood the article and the authors’ response letter correctly): During a marine survey, while the boat is moving, the chirp sonar fires a sequence of pings, whose echoes from the seafloor and deeper geological interfaces are recorded as usual. If anthropogenically knapped flint stones are on or underneath the seafloor, they start to hum, and the hum is recorded in addition to the echoes of the regular interfaces. The hum gets visible in the seismograms in form of signals plotting in the traveltime interval (“depth interval”) of the water column. This hum is missing if the rocks on or in the ground are natural or if there are no rocks. So far the claim.

For proving it, two things have to be shown:

(1) It has to be shown that anthropogenically knapped flint stones buried in sediment produce a measurable hum at all, and that natural rocks do not.

(2) It has to be shown that this phenomenon can be identified under field conditions.

So now, what have the authors shown, and what have they not shown that should have been shown to prove the claim?

As to (1) the authors mainly rely on their previously published work [41] and [51], [52], [53] cited inter alia in lines 236 to 239 and in connection with Figures 2 and 3.  It turns out that laboratory investigations on the acoustic resonance of lithics were performed on air where the lithics show some resonance peaks. The results are presented in form of spectra only. Time domain responses are not shown.

Whereas the authors expand on the lab experiments at length in the present article, the more relevant aspect of how buried lithics respond is touched only briefly. However, this is the relevant issue for field measurements. It turns out that this aspect was investigated with numerical simulations only (references [51], [52], [53]).  The numerical results are not shown or discussed in the present article. The numerical modeling presented in the cited articles shows that a response of the lithics is visible in the synthetic seismograms, but it is very small, indeed so small that it would hardly be noticeable in field seismograms.

The spectra of the synthetic seismograms show some damped remnants of lithic “resonance” lines, but no long lasting oscillations are observable in the synthetic seismograms (all that visible in Figures 7, 9, 10, 11 of [51]).  No “hum” can be identified in the time series.

My conclusion from these studies is that the resonance peaks of lithics observed on air in the lab do not play a significant role in reflection seismograms where the lithics are buried in a solid media (as was to be expected anyway). The effect is too small. And this effect was even overestimated in the cited studies because the numerical computations were performed for ideally elastic media and did not include viscoelastic absorption effects, which may however be quite strong in fine-grained marine sediments. So, from my point of view, the outcome the numerical modeling is clearly negative with respect to the goal of identifying artificially knapped lithics (as it was to be expected).

However, the authors do not discuss all these issues. Instead they expand on the measurements performed on air.

As to (2) the key-role plays Figure 7 of the present article. It shows the result of field measurements, for which the authors placed natural rocks and knapped rocks on and underneath the seafloor. The figure and experiment was published previous in their papers  [41] and [54]. The seismograms belong to an experiment with artificially knapped lithics placed on and underneath the seafloor. The records show (apparently) pre-causal seismic arrivals in the traveltime interval corresponding to the water column, which the author interpret as “hum” generated by the knapped lithics. The seismograms belonging to the natural lithics experiments do not show this sort of pre-causal arrivals (apparently). There are several points problematic and misleading in the line of the authors’ argumentation:

1. The cause of the observable “pre-causal” arrivals has not been investigated seriously. The observation is only “interpreted” as hum in the light of the on-air laboratory experiments, ignoring the rather negative outcome of the numerical modeling. Alternative explanations are not discussed.
2. For investigating if a broadband chirp signal can excite a hum in buried knapped flint rocks onsite it would have been necessary to perform measurements under well controlled conditions: anchoring the boat, measuring swell, measuring single records that are long enough to control the ground responses (Green’s functions) including multiple reflections (i.e. seismic arrivals bouncing back and forth between sea surface and sea bottom). This is to really understand the observed arrivals without and with artificial stone placements. For this purpose analyzing the waveforms of the signals and verifying the interpretation by numerical modeling are necessary.
3. Contrary to this, the presented records are not even long enough to see where and with which signal form and strength the 1^st multiple occurs. If the chirp would generate a significant hum it should start at the traveltime of the seabottom reflection and not beforehand. It should extend to increasing traveltime and decay over time due to absorption. In the seismograms it should be visible as what seismologists call a coda. A coda-type hum should also be generated by each of the following multiples. Nothing of this is observable in Figure 7. However, if the recording length is too short and the follow-up chirp is fired before the sequence of multiples has decayed, then the multiples of the previous chirps are recorded together with the follow-up seismogram. This would indeed be a mechanism for generating apparently pre-causal arrivals. To rule it out as a possible cause, records of sufficient length need to be presented.
4. One primary observable in this context is the reflectivity of the seafloor. It depends on the sediment sequence near the seafloor, the structure and arrangement of the lithics placed on and underneath it, their acoustic impedances, the surface roughness and seismic velocities. It can be expected that the placement of the lithics has a strong influence on the reflectivity expressed in reflection strength and waveform of the reflected signal. In the present and past papers of the authors – as far as I have seen them - no attempt has been made to investigate this reflectivity function following the state of art. Also the description of the experimental conditions is incomplete (size of the lithic packages, packing structure, surface roughness, results of the base measurements).
5. Indeed the supposed hum should be identifiable as part of the seafloor reflection response (which is the “reflectivity”, or call it Green’s function) as it would have its origin here. Instead, the supposed hum is considered to be a “haystack” feature “floating” apparently in the water column. However, if the “haystack” features were sort of hum, they should occur everywhere in the seismogram, not only in the time window belonging to the water column.
6. The only arrivals travelling back and forth in the water column are the multiples, but these cannot be analyzed properly, because the shown (or recorded?) time windows are too short. Changing the reflection strength of the seafloor through placement of differently dense packages of lithics would clearly have an effect on the strength of the multiples, too. At strong contrasts, the multiples can be repeated many times before they decay, and they can produce “haystacks” if the recording and firing sequences are too dense (see c).
7. The “haystack” features show a broadband signature, meaning they appear to have impulse-type waveforms (as far as this is recognizable in the figures). This does not fit to the idea of a more or less continuous hum composed of discrete spectral lines. Haystack waveforms need to be analyzed and compared to the chirp and seabottom reflections to clarify the situation.
8. Some of the haystack features show a diffraction-like traveltime move-out. This can be used to locate the diffracting structure.
9. Another item bothering me is that the authors do not provide information on their recording and processing parameters, neither in the present nor in their previous, here cited, papers. This disables any quantitative assessment of the results by the reader, and I find it not acceptable for a scientific paper. In Figure 7, for example, the seismograms are obviously displayed with different gains (visible through the different strengths of the technical noise, see the horizontal stripes). If row A would be displayed with the same gain as row C both rows might look not much different from each other.

So, regarding point (2) above, I do not see any proof that the supposed hum of knapped flint is real and an identifiable in-situ feature, and I do not see an explanation, why this hum – if it existed - should produce “haystacks” in the water column time window and nowhere else.

Just to put this right: I am convinced that the seafloor reflectivity is something worth to be investigated. It contains information on many features, among them the presence of rock packages. But I do not see a proof that it is possible to distinguish between anthropogenic and natural lithic packages, which is the central claim of the paper. 

One point, which should be mentioned finally, is that most of the presented material (maybe all?) was previously published, partly multiple times. I don’t know in how far this is acceptable for Remote Sensing, but the authors should make clear what aspects they consider new, or if they are just presenting a review article on their previous papers (some of which have already review character).

In summary, I have not come to a different conclusion than in my previous review and recommend the editors to reject the article because its central claim is not proved or made plausible in a scientifically sound and convincing way, and because the presented data interpretation are wrong in central aspects.

 

 

 

Reviewer 4 Report

The changes made by authors have improved the manuscript to some extent, but there are still some problems, especially in terminology and how the verification of results has been conducted and is described. Unfortunately, I cannot find convincing enough evidence that the HALD approach really works in practice as yet and, therefore, I see this manuscript as a working paper instead of a ‘comprehensive and authoritative reference on the subject’. My comments below for the author responses follow the initial numbering.

1. There is still great variety in terminology/expressions in various parts of the manuscript: in places (e.g. lines 33-37 in Abstract, lines 200-300, 339-340, 357-358, 520-521 in Results, lines 534-535 and 538-540 in Discussion and lines 603-606 in Conclusions) the authors seem already very certain and optimistic that the HALD approach really works even though the 'hard evidence' is still preliminary and most of the anomalous observations have not been properly verified on site. In a few other instances, they use more suggestive and cautious expressions (e.g. lines 103-105 in Intro), which would be much better suited in this manuscript (and especially in the current stage of development of HALD). This must be harmonised and the authors have to find a ‘happy medium’ describing the current stage of development and use it systematically throughout the manuscript.
2. The already published figures have not been removed or edited. As an addition to the previous comment and this one, I cannot agree with the authors that this manuscript would already stand as a ‘comprehensive and authoritative reference on the subject’. This is because it still presents so much preliminary and unverified data. Therefore, I see this merely as a working paper focusing on improved methodology and testing and the right moment for an authoritative reference paper will (hopefully) come sometime in the future. Please note that figure 2 contains text in Danish, which could be translated.
3. See my previous comment.
4. This is better now, but some essential information is still missing; for example, it is misleadingly presented whether the excavations have been conducted as part of this development work (for the purposes of anomaly verification) or previously (even several decades ago for some other purposes) and this has to be stated more clearly in the manuscript. More information could be included in the table, e.g., excavation years and references. Also, it must be stated more clearly if the site has been either diver-verified from the surface or via excavations/corings and a year when this has been conducted is also relevant.
5. I do not quite agree, especially the site maps are rather 'wild' and they could have been uniformed quite easily.
6. OK, it is satisfactory now, but various sections could have been harmonised more intensively.
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8. This is a better way, thank you.
9. OK, it is agreeable.
10. Yes, the table is much more informative format, but the manuscript is now even longer than the previous version; more information (see also comment no. 4) could have been included in the table so it would not have been necessary to include all the lengthy descriptions in the body text.
11. Why the testing in Sweden is not mentioned already in the Results section with the other test sites?
12. This is better now; more thorough exploration of the sediment type in question and its possible effects on the detection success ought to be taken into consideration and explored in the future, which could also be added in the Conclusions.
13. To me, this is one of the most fundamental problems in this work and I still cannot agree with the authors that the old fieldwork data could possibly provide sound enough verification base on the viability of this approach – there are simply too many uncertainties and margins of error to be taken into consideration (which are currently not critically discussed in the manuscript) and therefore verification via new fieldwork is essential. For example at the Lake Zürich cases, too many assumptions are made based on old excavation materials about the find density and depth in the sediment and this is not convincing. In addition, the authors have now added to the Roskilde Fjord results (line 410) that the sites are ‘precisely positioned’ – what does this mean or is this based as well to older fieldwork materials?
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