Peer review of: Arsenic contamination of Bangladesh aquifers exacerbated by clay layers (2020)



Reviewers' comments: 

Reviewer #1 (Remarks to the Author): 

What are the major claims of the paper? 

The authors make two claims, the first of which seems to be (both in the text and the title) the main 
focus of the paper: 

[1] Withdrawing water from (particularly shallow) Pleistocene aquifers in Bangladesh (and similar
environments) draws reactive organic carbon from clay layers within the aquifers promoting Fe(III)
reduction and consequent mobilisation of arsenic. Thus, such extraction makes (particularly shallow)
Pleistocene aquifers with nearby organic-rich clay layers prone to future increases in groundwater
arsenic.

[2] Recharge induced by groundwater pumping may protect low-arsenic aquifers in Bangladesh (and
similar environments)

Are they novel and will they be of interest to others in the community and the wider field? If the 
conclusions are not original, it would be helpful if you could provide relevant references. 

[1] Claim [1] as expressed in the abstract is not novel - as the authors point out themselves - the idea
having already been proposed by (Reference 15) Erban et al (2013) PNAS.
www.pnas.org/cgi/doi/10.1073/pnas.1300503110 and (Reference 16) Planer-Friedrich, B. et al. (2012)
Applied Geochemistry
doi:https://doi.org/10.1016/j.apgeochem.2012.08.005 amongst others, with the underlying
importance of the process of reactive organics in aquitards driving microbially mediated reduction
process in adjacent aquifers (albeit not with the same precise context) having been identified earlier
by (Reference 14) McMahon and Chapelle (1991) Nature.

[2] To the best of my knowledge, claim [2] is novel with respect to the particular arsenic-releasing
mechanism outlined in claim [1] - although the potentially arsenic-immobilising influence of relatively
oxidising, perhaps SO4 and/or NO3 rich, surface waters has been widely known for many years - and -
in contrast - the converse role of reactive organic carbon contained within such surface-derived waters
has also long been muted as a driver of arsenic mobilisation (Harvey et al., 2002, Science).

Is the work convincing, and if not, what further evidence would be required to strengthen the 
conclusions? 

The reported work supporting claim [1] is very convincing, supported in particular by compelling 14C 
and 3He/3H data as well as plausible back-of-the-envelope calculations as to the potential magnitude 
of the FeR and arsenic mobilisation impacts of the clay-later derived organic carbon that might be 
released. 

Claim [2] is rather more speculative and the evidence presented for it in the manuscript is not, in my 
opinion, very strong given the likely 3-D heterogeneity of the studied aquifer system, the multiple 
biogeochemical processes involved and the reliance on a relatively restricted field area. 

On a more subjective note, do you feel that the paper will influence thinking in the field? 

As a generally very well written account of a carefully designed research programme aimed to explain 
secular changes in well water arsenic in a studied well, this is an interesting case study that supports 
the importance of reactive organic carbon in (clay) aquitards in controlling the mobilisation of arsenic 
in immediately adjacent aquifers. 
 
Of particularly importance is that the authors have highlighted that the main mechanism proposed is 
most applicable to SHALLOW Pleistocene aquifers - and that is a very useful practical message - whilst 
it may also be inferred from the manuscript that application to predicting secular changes in DEEPER 
Pleistocene aquifers would NOT result in robust predictions - indeed I would suggest that the potential 
dangers of doing this should be made clearer in the manuscript. 
 
Further questions and concerns about the paper. 
 
Much of the discussion is based upon the assumption that all the studied Pleistocene aquifers were 
"orange" not "grey" - this seems highly speculative and based on little evidence - the follow argument 
is not very convincing in that regard: "In spite of differences in color, the drill cuttings indicate that 
the entire Pleistocene aquifer in the 40-70 m depth range, composed today of both grey and orange 
sands, was probably deposited and subsequently flushed under similar conditions and therefore 
uniformly orange." 
 
The use of the term "groundwater age" needs to be qualified - see for example the incisive 
commentary on this by Bethke and Johnson (2008) Annu. Rev. Earth Planet. Sci. 2008. 36:121–52 
 
The observed change in well water arsenic seems to have occurred at most over a matter of years - 
this timescale seems faster than any of the advective or diffusive or other mechanisms proposed - 
although the arguements are otherwise highly plausible, this would seem to somewhat undermine the 
main claim of the manuscript and, in any event, this is a point that should be substantively addressed. 
 
 
 
Appropriateness and validity of any statistical analysis 
 
 
Reviewer #2 (Remarks to the Author): 
 
Dear Editor, dear authors 
 
The subject of the manuscript is the potential (near-)future contamination by As of groundwater from 
relatively shallow Pleistocene aquifers. The investigated aquifer, and the type of aquifer for which the 
conclusions are most relevant, are in specific aquifers which are typically within the shallow-most 
oxidized zone. These Pleistocene aquifers host the screens of an increasing number of private tube 
wells. Drillers have learned to install screens of drinking water wells in orange sands rather than in 
grey sands. In fact, they have learned to do so by other excellent works of authors from this same 
group. 
 
The authors present data which indicate a risk of As contamination due to reductive dissolution of As-
hosting iron oxides by DOC released from a low-/semipermeable sediment unit capping the studied 
shallow Pleistocene aquifer. They provide evidence that the risk is due to an increased downwards 
hydraulic gradient due to groundwater extraction for Dhaka’s water supply. 
 
Albeit from just one field site, the manuscript contains several data types, obtained from four well 

nests installed in the area, for example: hydraulic head, arsenic conc. dynamics during about six-
seven years, general major chemistry, stable isotopes of water and carbon, tritium and tritium/helium 
dating, 14C dating of sediments, DOC and DIC, wet chemical extractions of drill cuttings. Indeed, the 
conclusions are reasonably well documented by the data but still the presentation need to be 
improved and need to be more focused. For example, it should make a reader able to clearly identify 
evidence in the form of hard facts (e.g., isotopic data, etc.) from softer/discussion points (e.g. 
downwards DOC loading amount and timing, and whether the variable elevation of the clay-to-sand 
interface makes up for an otherwise small DOC loading). 
 
While, of course, pointing out a potential risk is important, so – I believe – is it for nat. comm. that 
this risk is real and reasonably likely to occur (not necessarily a ‘ticking bomb’ but something in that 
direction though). My first of two major concerns is related to how well the ‘DOC transport’ step in the 
cause-and-effect chain (pumping>increased downward hyd. grad.>DOC transport>iron oxide 
reduction>As release) is adequately clearly proven. Importantly, this may be just a question of 
presentation though (See ‘major issue 3’ below). 
 
Nevertheless, there’s currently some speculation (lines 227-230) regarding the effect of the variable 
elevation of the clay-to-sand interface in this area. If this is maintained in a revised version then I 
propose this should be backed up by some hydrological (vertical 2d?) transport modelling of dispersion 
should be applied, taking into account the horizontal groundwater movement due to Dhaka’s pumping. 
Which dispersivities are required in such a model to create the mixing depth intervals inferred by the 
data? Are these dispersivities reasonable? Without significant dispersion, flow lines in a confined 
aquifer would be quite nicely parallel to the upper and lower boundaries of the aquifer no matter its 
variation. The flow lines wouldn’t follow a specific elevation above sea level. But see my remaining 
comments – as I see it the authors could work around this issue in another way. 
 
My second concern is related to the relevancy outside the specific field site. A previous study (Mihajlov 
et al., 2015, WRR) by authors of the same group was conducted with at least much of the same data 
types available and from a more extensive area (~25 km2) comprising the smaller study area of the 
current study. In Mihajlov et al., none of the samples from <90 m depth showed “evidence of As 
intrusion from the shallower depths”. I know that this is not the same as leakage of clay pore water 
and its DOC (and/or As?; see ‘Minor issue 3’). Yet I assume the authors would have made a careful 
statement in Mihajlov et al. if they sensed a risk of contamination by DOC which could challenge their 
statement. In Mihajlov et al., the few samples that had As concentration ≥10 µg/L were from gray-
tinted aquifer sands (i.e., classified as not-orange) and apparently must have been classified as such 
at the time of well installation, as the samples apparently stem from actual drinking water wells. The 
conclusion in Mihajlov et al. therefore may appear to be in contrast to the conclusion of the present 
manuscripts. I acknowledge that there may be a difference between the data available to Mihajlov et 
al. back then (2015) versus now to the authors of the present manuscript. However, the authors 
should still clarify why conclusions regarding DOC leakage from clay units capping the <90 m 
Pleistocene aquifer could not be made by Mihajlov et al. (2015). Were the data required to make at 
least a minimum assessment of the risk not available to Mihajlov et al.? Perhaps this clarification can 
even be used to constrain the proposed risk, which would be a good thing. 
 
If my above concerns can be dismissed by good arguments by the authors, and if the list of major and 
minor issues below can be dealt with in an appropriate manner, then I will strongly recommend that 
their work is published in Nat. Comm. In other words, formally I recommend the Editor to accept with 
‘major revisions’. 
 
Groundwater arsenic is more than deadly enough to justify publication (also in nat. comm.) even if it 
does not affect directly the 100,000s >150 m deep wells, but ‘only’ the numerous (how many?) 

‘shallow’ low-As wells. For example, each of these shallower wells will need monitoring and probably 
the drilling of a deeper well in the future. These wells also are more likely private than the deeper 
wells, and this may limit the accessibility (legal) and economy required for proper monitoring, so new 
management systems need to be implemented. 
 
I am sorry for my long review text – it could probably be boiled down to much much less, but I hope 
my points make it through anyways. I also would like to apologize beforehand for any 
misinterpretations made by me, as annoying they can be to have to defend then for the authors. 
 
Finally, I sincerely hope and trust that the authors, a very strong group which I respect very much, 
will be able to adjust their manuscripts to make it an excellent and very important contribution to nat. 
comm. 
 
Best regards 
Søren Jessen 
 
 
Major issues: 
1. The manuscript ‘sets the scene’ nicely, but simplifies things too much by inferring direct relevancy 
to the 100,000s >150 m deep wells (lines 41-47, 121-122), while in fact the study addresses/collects 
data from a ‘shallow’ Pleistocene low-As aquifer. These are very important differences. The relevancy 
for the aquifers directly targeted should be made crystal clear from the beginning. I acknowledge that 
the summary (lines 274-276) do make this distinction but that is too late in my opinion. The notion in 
the abstract (lines 23-24) that by ‘Pleistocene’ the authors mean ‘>12 kyr-old’ is too subtle. 
Some elaboration on this type of aquifer could be made. The studied oxidized aquifer may be 
Pleistocene in age by definition but at the same time it is younger than the last glacial maximum (LGM) 
during which the deepest Pleistocene aquifers likely became oxidized. The studied aquifer is therefore 
a ‘post-LGM Pleistocene aquifer’, and as such it is composed of much younger aquifer material, and its 
non-oxidized parts contain younger and more reactive organic carbon (and perhaps more mobile As) 
than the deeper and more flushed (pre-LGM) Pleistocene aquifers. The 14C sediment dates combined 
with BGS’s old report’s Fig. 3.4 indicates that perhaps “Hiatus 2” caused the oxidation of the studied 
aquifer sand during a few thousand years maximum (I’m no geologist, but… ‘preboreal oscillation’)? 
This affects for example lines 108-110 and elsewhere. 
 
2. Is the carbon from the capping clay unit driving the As release from the confining unit? It most 
probably is, but the supporting data should be highlighted much more. For example, the similar 14C-
age of DOC in the capping clay and the sand just below it vs. in the Holocene aquifer is not easily 
accessible to the reader. This is a hard fact, and should be presented as such, earlier in the text (than 
lines 204-208, repeated at 244-245, and 969-974). In general, all the hard facts (hydr. gradients, 
increase in As in 41 and 51 m depth, reactive DOC, water stable isotopes, other isotopic data, etc.) 
should be presented earlier and in the main text rather than in supporting info. 
Graphs of d-excess (= delta2H - 8*delta18O) vs. depth should replace 2H graphs. Interpretations of 
stable isotopes of water are usually made relative to the GMWL. Use of d-excess enables just that 
without the need for showing a delta2H vs. delta18O-plo. On the other hand the visual appearance of 
the 2H-vs.-depth plot does not directly add information because it will appear almost like the delta 
18O-vs.-depth plot. Lowered (from ca. 10) or even negative d-excess results from evaporation. 
 
3. Much of the manuscript discusses the possible transition of orange sands to grey in the upper part 
of the Pleistocene sand (lines 122-125 and elsewhere). The discussion is supported by reasonable but 
many and a bit discussion-prone back-of-the-envelope calculations. However, I don’t see this redox 
state transition as necessary for the story: A transition to grey may be ‘modern’, or it may have 

occurred as result of DOC diffusion during thousands of years, or the sand may have been deposited 
as oxidized and turned grey shortly after such as the Holocene deposits are now, so that no sea-level-
linked transition ever occurred, or a combination of some of these. In any of these cases no one can 
take away the fact that right now arsenic concentrations are increasing, so it MUST be a modern 
phenomenon taking effect. The increasing As concentrations is the smoking gun of the story. Isotopic 
and other evidence further strongly indicate that leakage containing DOC from capping clay is the 
reason for this. Yes, the DOC becomes mobilized into a now grey (Pleist.) unit, but even so, and even 
if the unit is ‘young Pleistocene’, the unit’s organic carbon is relatively old and unreactive due to 
flushing and the addition of more reactive org. carbon is totally likely able to mobilize arsenic (again?) 
from these sediments. 
Along these lines, with the right argumentation neither the speculation in lines 227-230 nor the above 
proposed modeling may be necessary at all. This would help focus the paper. 
Other options that would aid focusing the paper, and which the authors might consider are to (i) 
eliminate the Ca profile from Fig. 2 and the text dealing with it. Instead Fig. 2a could be increased in 
width; (ii) eliminate the color coding of the M-wells in Fig. 3. It shouldn’t be important anyway, as 
they show the same trends (don’t they?); (iii) perhaps aggregate data in depth-categorical plots, with 
categories like: ‘Holocene reduced aqf.’, ‘Capping clay’ (of Pleist. aquifer), ‘Upper reduced Pleist. aqf.’, 
‘Oxidized Pleist. aqf.’, ‘Lower reduced Pleist. aqf.’; ‘Lower Pleist. clay’. If, for example, horizontal box 
plots were shown, statistical significance could be evaluated more easily by eye, or (iv) Fig. 3 could 
adapt the clever color coding of Fig. 2; (v) with focus only the capping clay and the Upper reduced and 
oxidized sand of the Pleistocene aquifer, all concentrations could be shown relative to the distance 
above/below the clay-aquifer-interface. 
As all data goes into tables in the Extended Data, and as more detailed graphs can be provided also in 
ED where necessary, the simplification in the main figs. and text will only help communicate the main 
message. 
 
4. The authors should present arguments that the case they present in the present manuscript is likely 
relevant across a much wider area, i.e. an area that extends even outside the 25 km2 area of Mihajlov 
et al. (2015). This could (not necessarily ‘should’) include a figure/map, although some display of the 
distribution of Pleistocene ‘shallow’ low-As wells in Bangladesh delta indeed would be a major 
improvement to the manuscript, and increase its use in the future. 
 
5. In the calculation of reactive DOC diffusion, the concentration gradient of the reactive DOC should 
be used; not the concentration gradient of total DOC (Lines 1022–1025 + 1113). Of course – one may 
then question the method by which reactive DOC was measured (one month reaction time within a 
filtered sample vs. some years in the subsurface with contact to solids and ‘stuff’) and from that 
dismiss this way to quantify reactive carbon. 
 
Minor issues/questions: 
1. Figs. ED2a (% Org. C) and ED7: Very important figures; shouldn’t they be in the main text? 
 
2. Line 115: Is there any grain size difference between pre-Holocene vs. Holocene aquifer sediments? 
 
3. Lines 131-134, Fig. ED3d (PO4 extractable As): (i) The main point with the figure I think would be 
to indicate that ‘yes, mobilizable As is present in all depths – with the addition of reactive carbon, we 
may expect an As release’. With that as the only take home message, its displayed depth distribution 
shouldn’t be given much (if any) attention. Now the figure seem to be include more or less just 
because it was measured. For example (ii) the symmetric feature of the depth-distribution is noted but 
actually not used in the interpretation or if it is, it is not clear how it is used. (iii) Also, if we chose to 
pay close attention to the actual values, then one could as well note that as much As can be mobilized 
from the capping clay as from the upper Pleist. grey sand. So, how (if) is it possible to distinguish 

whether the As release take place in the Pleist. reduced aquifer (as proposed) or in the capping clay? 
Perhaps via the indicators of mixing (e.g., stable isotopes of water and Cl values)? 
In my opinion, the distinction in (iii) above is not necessarily important. In both cases org. C from clay 
remains the driver for As release. Whether lowered hydraulic pressure induce leakage that carried 
DOC into the Pliest. aquifer or leakage that carried As released within the clay, is not pivotal. 
 
4. Lines 135-136: (i) The origin and direction of reactive org. carbon could be from below as well as 
from above. Fig ED2a (% Org. C) ends right below the oxidized aquifer, so a source may exist deeper 
than the graph which we just don’t see. The sentence somehow infer that we know the direction of 
groundwater flow during the last 20,000 years, which I don’t think we do – it may have been upwards, 
depending on location of channels at the surface. (ii) With the text ‘that turned orange sand to grey’ it 
is inferred that a reduction of a deep oxidized (i.e., sea level related) sediments actually occurred. I 
don’t think we can be sure that the sand did not just become grey very quickly after deposition, like 
the Holocene (and today's) sediment did (do) and was never oxidized after that. (iii) Delete last 
instance of ‘that’. 
 
5. Lines 240-242: Please elaborate, e.g. how important is this mechanisms thought to be in these 
other areas? 
 
6. Lines 181-183: hard to evaluate for the reader. Statement seems a little too ‘bombastic’. I suggest 
to soften it – or do the above mentioned box-plot option, which might reveal the clearest trend and 
ease its communication. 
 
7. Line 169: Please clarify, ‘is not responsible’ for what? 
 
8. Fig. ED7: Please change units to mM to become consistent with text. 
 
9. Line 267: Please use 'Because' instead of ‘As’, not to confuse this ‘As’ with ‘Arsenic’. 
 
 
 
Reviewer #3 (Remarks to the Author): 
 
This manuscript on possible in-aquifer exacerbation of arsenic release via clay layers in Bangladesh is 
thorough, well-written, well-designed and the implications are significant – particularly with regard to 
the protection, or otherwise, that clay layers above lower As Pleistocene aquifers may give. In general 
the manuscript seems worthy of publication in Nature Communications. Some points which would 
benefit from further consideration or clarification: 
 
- It would be helpful to show more characteristics of what this “reactive carbon” source actually is. As 
far as I can tell, “reactive DOC” here is simply defined as a difference in DOC between unacidifed for 1 
month and immediately acidified subsamples (around line 941). Is this really a sufficient proxy for 
“reactive DOC”? This seems a rather big assumption, particularly as it is clear from other studies that 
not all types of DOC contribute to arsenic release comparably. How do these estimates of “reactive 
DOC” compare with other bioavailability proxies? 
 
- The evidence presented strongly supports that contributions from the in-aquifer clay layer are 
contributing to arsenic release here. But do we know what exactly from that clay layer is driving this 
process? The contribution of potential methanogenesis is mentioned (lines 980 – 985) – is there any 
direct evidence to support this? (e.g. dissolved methane measurements?) 
 

- The heterogeneity of the sub-surface clay layers seems of key importance here, as the authors 
acknowledge. If drill cuttings of 4 well nests within a 100 m radius indicate a 6 – 13 m thick clay layer, 
it seems plausible that this clay layer could be very thin, or even missing entirely, in nearby areas too 
(it is mentioned that the layer is missing 500 m south). Would it be possible that these fast tracks 
introduced by such windows in the clay layer could contribute surface-derived organics and modern 
recharge that contribute to the conditions seen here (e.g. tritium increases at 60 mbgl, mixing lines 
shown on Extended Data 5)? Can this be ruled out?