of 20
Reviewers' comments:
Reviewer #1 (Remarks to the Author):
This manuscript addresses the root cause of MR relaxation of water protons due to spatially
-
varying
magnetic fields. To date, the distribution of these fields from sources such as iron oxide nanoparticles
has been difficult to empirically establish, leadin
g to inferences drawn from modeling or from the
macroscopic effects of these fields on the proton relaxation rate.
The authors employ a novel technique to map these magnetic fields using NV
-
center magnetometry to
achieve sub
-
micron resolution. In additio
n, they localize magnetic field sources and use Monte C arlo
simulation of the same to predict the macroscopic relaxation rates from their mapped fields. These
techniques are then tested on two models: iron uptake by macrophages, and iron overload in the li
ver
of a murine model.
It would be valuable to expand this line of research to look at other types of field sources that may not
be as "well
-
behaved" as these particular IONs. For instance, these particles do not appear to be
strongly interacting, are of
fairly large size (200 nm diameter), and the behavior at clinical field
strengths can be predicted by extrapolating measurements made at the DC bias field of 10 mT by use
of the M vs H curve. However, in vivo iron may or may not exhibit similar behaviors,
especially if not
superparamagnetic.
Of critical importance is the distribution, geometry, and magnetic order of in vivo iron, such as ferritin
and hemosiderin. Additionally, the use of iron
-
based contrast agents already on the market for clinical
use (
e.g., Feridex, Feraheme) or pre
-
clinical would be useful. Knowing how well the techniques
described in the manuscript extend to these cases would be valuable. Smaller particles with different
magnetic ordering might not generate sufficient magnetic field f
or NV
-
center detection (17 nT
sensitivity reported here). This could be briefly visited in the discussion, or saved for later work.
The paper is well
-
written, with an appropriate distribution of information contained in the main text
and in the supplemen
t.
Line 208
-
please define ODMR as optically
-
detected magnetic resonance. I don't believe it is defined
prior.
Line 286
-
287
-
The free water diffusivity at 12.9 °C can be predicted from the Speedy
-
Angell fit in the
Holz paper. However, this value is lik
ely higher than the extracellular diffusivity. The intracellular
diffusivity was set to 1/3 of the extra cellular diffusivity (as currently listed) without justification. What
effect might changing these have on the MC results? You might also mention that
your MC simulation
assumes a purely outer
-
sphere
-
like relaxation mechanism, i.e., there is no residence time on the
surface of the IONs.
Reviewer #2 (Remarks to the Author):
The paper by Davis et al. uses NV magnetometry to image the local magnetic
field within mammalian
cells produced by known MRI contrast agents. The goal is to exploit the higher resolution of optical
microscopy and the detailed knowledge of the magnetic field within the cell to more precisely predict
the macroscale MRI contrast.
The overall science seems sound but I am a bit skeptical on the novelty and overall impact. The
application of NVs to determine the magnitude and direction of external magnetic fields has already
been demonstrated extensively in a variety of settings (I a
m sure the authors know the literature in
this area is vast). In particular, ensembles of near
-
surface NVs (identical to those used in this work)
have been exploited to image cell with sub
-
cellular resolution, not only by the Walsworth group (listed
as Ref
s 13 and 14) but also by others (e.g., Magnetic spin imaging under ambient conditions with sub
-
cellular resolution, Steinert et al., Nature C ommun. 4, 1607 (2013)). The authors indicate that none of
these experiments were carried out in mammalian cells and
that no connection with MRI contrast was
made before. However, since the presented results are also a proof of principle, I am not fully
convinced this work represents a major step. In particular I don't see (in practice) a strong case on
how to transitio
n from the comparatively
-
lower
-
resolution of MRI images to NV magnetometry or vice
versa (in Fig. 3 the authors ultimately have to excise a section of the liver). Something similar can be
said about Fig. 4 where high
-
resolution microscopy is possible thank
s to the NVs but no direct
comparison can be made with MRI. Finally, at times I found the overall presentation unnecessarily
obscure to the non
-
expert, particularly in the abstract and introductory section (e.g., statements such
as “this technique can foll
ow the magnetic consequences of a dynamic process in living cells” or others
similarly confusing are not particularly helpful to guide the reader).
Reviewer #3 (Remarks to the Author):
The authors have developed methods to directly map subcellular m
agnetic fields in live and fixed
mammalian cells and tissues, using nitrogen vacancy (NV) microscopy, and have then used these
microscopic fields to accurately estimate macroscale T2 relaxation times.
The methodology is novel and would be of interest to
others in the community. The ability to
accurately estimate T2 relaxation times from microscopic magnetic field measurements would be of
value in understanding MRI contrast as well as in the development of improved MR contrast agents.
The work is relativ
ely convincing, although I have a number of questions and requests for clarification
that I believe would improve this work and make it more convincing. I have also made comments in a
few places that are intended to improve the ability for other researcher
s to understand and replicate
the work.
Specific C omments
Page 3 line 35: “the resonance frequency of these transitions shifts linearly”. Can the authors be more
clear about how they are exploiting this Zeeman
-
based shift in resonance frequency?
Page
4 line 52: “and an in vivo model”. This is an overstatement and I’d like the authors to change the
wording so as not to mislead the readership. The authors have NOT demonstrated in vivo NV
microscopy, and yet the wording in the paper could easily be misin
terpreted this way. The model of
iron load to the liver of mice is of course and in vivo model, but in my opinion not worth explicitly
using this phrase “in vivo” here, since it is obvious that it is an in vivo model (as with any other mouse
model is). All
that the authors have demonstrated is the ability to map fields in excised histological
tissue sections
.
Page 4 line 64: “10mT”
is this field high enough? What other aspects of this bias field are important?
Authors should comment on the optimal streng
th and characteristics (such as uniformity) of the bias
field.
Page 4 line 66: “superparamagnetic IONs”
authors should describe these IONs in enough detail that
others could replicate their experiments.
Page 4 line 70: “field profiles ... cannot be dir
ectly observed by conventional EM”. Granted that is true;
however, EM or perhaps other forms of microscopy could be used to locate particles, even within cells,
and then local fields could be accuratley modeled around these particles based on the known phy
sics
of superparamagnetic particles in the presence of a bias field. T2 relaxation could then be predicted in
the same way that the authors are doing here. So in other words, I think the authors may be
overstating the importance of NV microscopy as a way o
f predicting T2 relaxation. I’d like the authors
to discuss this, either here or in Discussion or both.
Page 4 line 72: “after incubating them ...”
authors should provide data about the loaded cells, e.g.
the loading level in units of pgFe/cell, any othe
r characteristics of potential relevance and interest to
readers involved with cellular MRI.
Page 4 line 79: “3D maps of magnetic field sources in the sample”
these maps should correspond to
maps of ION particle location / size, I believe, and could be
validated using EM or other microscoyp of
the same samples / cells. I would like to see validation of this type. C an authors do this and comment
on this?
Page 5 line 84: “Then, the off
-
diamond height (z) ...”
this seems like a potentially very ill
-
posed
problem. Authors should show an analysis of this. For example, it sounds like it would be difficult to
distinguish a different size particle from a different z
-
height. If the ION cores are not monodisperse
(and they usually aren’t) then this seems like it
could be a significant problem to me.
Page 5 line 98: “Importantly, since this information ...”
-
But is it possible to make NV measurements
and T2 measurements on the same sample? Also, how many cells (or what density of cells) can be
measured with the N
V method?
Page 5 line 101: What was a 1:1 mixture necessary and what would the consequences of using a
different mixture be?
Page 5 line 104: “Monte Carlo prediction”
-
It is unlikely that cells are arranged in such a regular
cartesian grid of equal
-
si
zed spheres. Authors should comment on the changes in T2 that arise from
irregular distribution and size of cells.
Page 5 line 106: “concentration of IONs”
-
However, T2 could have been predicted from knowledge of
particle location/size within a cell, wh
ich might for example be measurable by EM or other light
microscopy. The same Monte C arlo prediction of T2 could be done from this knowledge, which would
therefore not require NV microscopy. Authors need to justify why NV microscopy is necessary for
unders
tanding the basics of T2 in ION
-
loaded cells.
Page 5 line 110: Fig. 2f
the figure is labeled "clustered" but this is ambiguous. IONs could be
clustered extracellularly or could be confined / clustered inside sub
-
cellular compartments. I believe
these t
wo situations should yield different T2 values but the authors should comment. Also, how did
their simulations deal with the barriers / restrictions to water motion introduced by sub
-
cellular
compartment membranes? One relevant simulation that I’d like to
see would be to show simulated T2
values for extracellularly clustered Fe particles, and to compare to intracellularly compartmentalized
Fe particles.
Page 5 line 118: “900nm”
why so large? Is NV measurement / microscopy not possible using more
convent
ional IONs? This is not a particle size that is commonly used for in vivo “clinical” applications of
IONs.
Page 5 line 123: “punctate”
doesn’t look punctate to me in Fig 3c. In fact the images in Fig 3c are
quite poor
I don’t recognize structures in
the fluorescent images (they are very poor quality) and
don’t understand what correlations I’m supposed to be making between the magnetic field maps and
those fluorescent images. Authors need to improve image quality and make those correlations more
clear.
Page 5 line 138: “This allowed us ...”
-
Similar to a comment above, why is it not possible to perform
source localization in this situation
-
that would be more informative and would allow a more direct
validation against optical or EM, and more direct c
onfirmation that "clustering" or sub
-
cellular
compartmentalization is being measured.
Page 5 line 145: Discussion
-
This Discussion is very brief. I would like to see more, such as a more
detailed discussion of limitations (such as the ill
-
posed nature o
f source localization and why source
localization was not performed on the tissue samples), also comparison to any other technologies for
microscopy of magnetic fields such as microSQUID, discussion of sensitivity, spatial resolving power
for sources, and
temporal resolution.
Page 8 line 174: “unknown”
why is this not known? Seems like it would be important to know this,
to allow others to replicate this work. Authors should clarify.
Page 9 line 207: “sufficient out
-
of
-
plane field strength ...”
athors
should be more clear about what
this means
-
how much is "sufficient" and what are the specifications / tolerance limits for this bias
field uniformity or other characteristics.
Page 9 line 208: “ODMR”
this acronym has not been defined.
Page 9 line
215: “quadratic background ...”
how is bias magnet inhomogeneity corrected for at the
source localization stage?
Page 9 line 221: “sensitivity”
how was this sensitivity determined? It is good to see this sensitivity
expressed in units of ION particles
that can be detected at a given spacing off the diamond; however,
commonly used IONs have iron oxide cores of 3
-
5nm, not 200nm. Authors should express sensitivity
in units of these common IONs since that is where the general interest would lie. If this NV
microscopy
method is not going not able to sense conventional 3
-
5nm ION cores, then this is a significant
limitation that needs to be discussed.
Page 9 line 223: “200nm”
does this refer
to the iron core size? If so, that seems too large compared
to st
andard/practical IONs commonly used for cell tracking.
Page 9 line 227: “the bias field was aligned ...”
not clear why this was done, and why the same
method as in the cellular imaging (with bias field parallel to plane of NV layer) could not be used.
Page 11 line 285: “12.9degC”
seems like a pretty cold temperature. Why was this particular
temperature used?
Page 11 line 285: should also specify intrcellular/extracellular volume fractions.
Page 11 line 288: should specify units of the bulk spin ma
gnetization; the summation implies that this
is unitless but does that make sense?
Page 12 line 294: “Data presented ...”
can the authors justify that these numbers in this sentence
are large enough?
Page 12 line 308: “multi
-
echo spin echo”
was this a C PMG sequence? Authors should be more clear.
Authors should comment on the fact that T2 measurements will depend on echo spacing in this kind of
measurement.
Page 12 line 309: “T2 relaxation ...”
this
seems to imply that the signal decay was not
monoexponential. Authors should clarify. Also, the same may have been true for the simulated NMR
signal decay and should be commented on also.
Page 12 line 312: “unsupplemented ...”
were these live or fixed c
ells? If live cells, wouldn't the IONs
have been taken into the cells over time?
Page 13 line 328: “to seal ...”
does this imply that a vacuum was used to force the tissue against the
diamond? If so, authors should be more clear.
Page 13 line 331: “sin
gle NV axis”
which axis specifically?
Page 13 line 332: “This strong ...”
why wouldn't this strong bias field have been used for all
experiments, not just this one? Seems like it would be produce stronger fields and therefore better
measurement precisi
on.
Page 18 figure 3 caption: “a, h and i”
I don’t see these labels.
Page 19 figure 4: Is it not possible to show optical (e.g. brightfield) images at all the same time points
as the magnetic field images? Authors should specify how large scale bars
are.
Page 19 figure 4 and associated text in the main body: Is it not possible to localize magnetization
sources in this situation of tissue sample (like they did for cell samples?). If not, why not?
We
thank
the referees for their
overall
enthusiasm and constructive comment
s, which have helped improve
this
manuscript.
Author responses are provided below in blue text. Revisions to the manuscript are also
highlighted with blue font.
Reviewe
r
#1 (Remarks to the Author):
This manuscript addresses the root cause of MR relaxation of water protons due to spatially
-
varying
magnetic fields. To date, the distribution of these fields from sources such as iron oxide nanoparticles has
been difficult
to empirically establish, leading to inferences drawn from modeling or from the macroscopic
effects of these fields on the proton relaxation rate.
The authors employ a novel technique to map these magnetic fields using NV
-
center magnetometry to
achieve su
b
-
micron resolution. In addition, they localize magnetic field sources and use Monte Carlo
simulation of the same to predict the macroscopic relaxation rates from their mapped fields. These
techniques are then tested on two models: iron uptake by macrophag
es, and iron overload in the liver of a
murine model.
It would be valuable to expand this line of research to look at other types of field sources that may not be
as "well
-
behaved" as these particular IONs. For instance, these particles do not appear to b
e strongly
interacting, are of fairly large size (200 nm diameter), and the behavior at clinical field strengths can be
predicted by extrapolating measurements made at the DC bias field of 10 mT by use of the M vs H curve.
However, in vivo iron may or may
not exhibi
t similar behaviors, especially
if not superparamagnetic.
Of critical importance is the distribution, geometry, and magnetic order of in vivo iron, such as ferritin and
hemosiderin. Additionally, the use of iron
-
based contrast agents already on
the market for clinical use (e.g.,
Feridex, Feraheme) or pre
-
clinical would be useful. Knowing how well the techniques described in the
manuscript extend to these cases would be valuable. Smaller particles with different magnetic ordering
might not generat
e sufficient magnetic field for NV
-
center detection (17 nT sensitivity reported here). This
could be briefly visited in the discussion, or saved for later work.
Thank you for this comment. Since the focus of this manuscript was on developing the basic met
hodology
for connecting microscale magnetic fields with MRI signals, we used
macrophage uptake of
well
-
behaved
magnetic materials as our
primary model to facilitate detailed experimental validation of this method.
However, we agree that in future studies it will be important to extend the capabilities of this technique
beyond this basic scenario to less ideal magnetic materials
,
including biogenic iron. As suggested, we have
expanded our discussion of the need for
these future experiments and the technology improvements
needed to make such measurements possible. This text appears in the updated manuscript on lines
1
7
5
to
196
.
The paper is well
-
written, with an appropriate distribution of information contained in th
e main text and in
the supplement.
Thank you!
Line 208
-
please define ODMR as optically
-
detected magnetic resonance. I don't believe it is defined prior.
Thank you
. The definition has been added
on line
25
3
in the revised manuscript.
Line 286
-
287
-
The free water diffusivity at 12.9 °C can be predicted from the Speedy
-
Angell fit in the Holz
paper. However, this value is likely higher than the extracellular diffusivity. The intracellular diffusivity was
set to 1/3 of the extra cellular d
iffusivity (as currently listed) without justification. W
hat effect might changing
these have on the MC results? You might also mention that your MC simulation assumes a purely outer
-
sphere
-
like relaxation mechanism, i.e., there is no residence time on
the surface of the IONs.
Thank you for
this comment
.
Our diffusion model
is based on the
work
of
Pfeuffer et al
1
, who
found that
extracellular water
is well approximated
by
the bulk
water
self
-
diffusion coefficient
, and that the intracellular
self
-
diffusion constant
is
approximately 1/3 that of bulk water
.
The effect of cell membrane
s
and the
geometric arrangement of cells is explicitly include
d
in or cellular lattice model
, in which the
cell membranes
are treated
as semi
-
permeable barriers to water.
This modeling approach produced experimentally
validated results in
a
recent
study of
cellular
water
diffusion for MRI
reporter development
2
.
The relevant
citations have been added to the text on line
s 356
-
360.
We have
also
added a comment on the assumption of purely
outer
-
sphere relaxation
on lines 345
-
346
.
Thank yo
u for very much for your
review.
Reviewer
#2 (Remarks to the Author):
The paper by Davis et al. uses NV magnetometry to image the local magnetic field within mammalian cells
produced by known MRI contrast agents. The goal is to exploit the higher resolution of optical microscop
y
and the detailed knowledge of the magnetic field within the cell to more precisely predict the macroscale
MRI contrast.
The overall science seems sound but I am a bit skeptical on the novelty and overall impact. The application
of NVs to determine the magnitude and direction of external magnetic fields has already been demonstrated
extensively in a variety of settings (I am
sure the authors know the literature in this area is vast). In particular,
ensembles of near
-
surface NVs (identical to those used in this work) have been exploited to image cell with
sub
-
cellular resolution, not only by the Walsworth group (listed as Refs
13 and 14) but also by others (e.g.,
Magnetic spin imaging under ambient conditions with sub
-
cellular resolution, Steinert et al., Nature
Commun. 4, 1607 (2013)). The authors indicate that none of these experiments were carried out in
mammalian cells and
that no connection with MRI contrast was made before.
Thank you for your comments. We acknowledge that our study builds on previous work by multiple groups
establishing the basic technology for
wide
-
field
mapping
of
magnetic fields near diamond surfaces,
which
we tried to convey appropriately in the introduction, including work done with mammalian cells
(e.g. r
ef 14)
.
We regret that we missed the Steinert citation due to our focus on DC magnetometry; we have added it in
the revised manuscript on line
s
45
-
48
and
197
-
203,
and discuss it further below.
The primary novelty of our study is the development of methods to make the connection between
NV
-
based maps of the microscale distribution of magnetic fields in biological samples with the contrast
seen in
conventional MRI. We believe this is an important new capability for the MRI field, and were happy
to see this view supported by most of the referees.
However, since the presented results are also a proof of principle, I am not fully convinced this work
r
epresents a major step. In particular I don't see (in practice) a
strong case on how to transition from the
comparatively
-
lower
-
resolution of MRI images to NV magnetometry or vice versa (in Fig. 3 the authors
ultimately have to excise a section of the live
r). Something similar can be said about Fig. 4 where high
-
resolution microscopy is possible thanks to the NVs but no direct comparison can be made with MRI.
Thank you for this comment. The primary evidence that the methods presented in this study effectively
connect lower
-
resolution MR images to NV magnetometry is provided in the detailed experiments presented
in Figures 1 and 2, as well as Supplementary Figur
es 2, 3, 7 and 8. In these experiments, we
focused on
demonstrating the core
capability of our method
using the well
-
controlled experimental scenario
of iron
oxide phagocytosis by macrophages
. This allowed us to prepare biological samples with different
ex
perimentally controlled distributions of magnetic materials, enabling us to establish and validate the ability
of NV magnetometry, 3
-
D magnetic field reconstruction, and Monte Carlo simulations of nuclear spin
precession to accurately predict MRI contrast.
This key demonstration is further reinforced in the revised
manuscript with the addition of several experiments suggested by Reviewer #3 (Supplementary Figs
7 and
8
).
The experiments shown in Figs. 3 and 4 are intended to demonstrate the potential for fu
ture
applications
in more complex or dy
n
amic contexts
. While we certainly agree that more work must be done
in the future to truly apply this technology to answer specific biological and clinical questions, we believe
the proof
-
of
-
concept
nature of the
exp
eriments presented in this manuscript are consistent with what has
been done in other high
-
impact publications in this field
(e.g.
3
-
8
).
We also thank the reviewer for pointing out the 2013 paper from Steinert
et al, which used NV
relaxation measurements to map the location of T
1
contrast agents near the diamond surface. We apologize
for omitting this citation in our original manuscript, and have a
dded a reference to it on lines
45
-
48
. We
have also added a discussion starting on line
197
about how this complementary method for evaluating T
1
contrast could be combined with the presented work on T
2
contrast to create a more complete picture of
potential MRI contrast sources in biological
specimens.
Finally, at times I found the overall presentation unnecessarily obscure to the non
-
expert, particularly in the
abstract and introductory section (e.g., statements such as “this technique can follow the magnetic
consequences of a dynamic proc
ess in living cells” or others similarly confusing are not particularly helpful
to guide the reader).
Thank you for this comment.
We
have revised the manuscript
as suggested
to provide more
precise
information to readers
(
e.g.,
lines
13
to
14 and 54
to
57
)
.
Thank you for your helpful comments.
Reviewer
#3 (Remarks to the Author):
The authors have developed methods to directly map subcellular magnetic fields in live and fixed
mammalian cells and tissues, using nitrogen vacancy (NV) microscopy, and
have then used these
microscopic fields to accurately estimate macroscale T2 relaxation times.
The methodology is novel and would be of interest to others in the community. The ability to accurately
estimate T2 relaxation times from microscopic magnetic
field measurements would be of value in
understanding MRI contrast as well as in the development of improved MR contrast agents.
Thank you for these comments
!
The work is relatively convincing, although I have a number of questions and requests for clari
fication that
I believe would improve this work and make it more convincing. I have also made comments in a few places
that are intended to improve the ability for other researchers to understand and replicate the work.
Specific Comments
Page 3 line 35:
“the resonance frequency of these transitions shifts linearly”. Can the authors be more clear
about how they are exploiting this Zeeman
-
based shift in resonance frequency?
Thank you. We have clarified this sentence to explain more precisely that the Zeeman energy difference
between the +1 and
-
1 states leads to the splitting of the 2.87 GHz resonance into two peaks, whose
separation from each other increases linearly with ma
gnetic field strength
(lines
36
to
38
).
Page 4 line 52: “and an in vivo model”. This is an overstatement and I’d like the authors to change the
wording so as not to mislead the readership. The authors have NOT demonstrated in vivo NV microscopy,
and yet
the wording in the paper could easily be misinterpreted this way. The model of iron load to the liver
of mice is of course and in vivo model, but in my opinion not worth explicitly using this phrase “in vivo” here,
since it is obvious that it is an in vivo
model (as with any other mouse model is). All that the authors have
demonstrated is the ability to map fields in excised histological tissue sections.
Thank you.
As suggested, w
e have
modified the text
to clarify that
we used histological specimens form
a
mouse model of hepatic iron overload
(line
s
54
-
57
and abstract.
)
.
Page 4 line 64: “10mT”
is this field high enough? What other aspects of this bias field are important?
Authors should comment on the optimal strength and characteristics (such as unifor
mity) of the bias field.
Thank you for this question.
To better explain our choice of bias field in the main text, we have added text
on lines
68
to
70 and 416 to 419
.
To further expand on this topic, s
electing a
b
ias field for vector
magnetometry of
superparamagnetic so
urces requires balancing
the need to magnetize the particles
with
the need to maintain
NV fluorescence contrast
, since
the
sensitivity of NV vector magnetometry decreases
at higher field strengths
. This effect is
due
to the quantum
basis of the NV defect shifting from along the
defect
axis
to along the applied field
, so that
m
s
is no longer an eigenstate of the spin Hamiltonian
at higher
field strengths
. The eigenstates of the spin Hamiltonian will be mixed states of m
s
=0 and m
s
=+/
-
1
, reducing
the contrast of the optically detected electronic spin resonance.
This was discussed
at length in Tetienne
et al
(reference
17
in the manuscript)
and
is
summarized
in
our
revised
SI section
on
SQUID Magnetometry
and Saturation Field Scaling
.
Page 4 line 66: “superparamagnetic IONs”
authors should describe these IONs in enough detail that
others could replicate their experiments.
Thank you. We have clarified in the main text that these are multi
-
core
superparamagnetic
200 nm
iron
oxide
particles (lines 78
-
79
), and added further information in the Methods, including the catalog number
of the particles (line
241
).
In addition, we have characterized the magnetic behavior of these particles using
SQUID magnetometry, as shown in Supplementar
y Fig. 2.
Page 4 line 70: “field profiles ... cannot be directly observed by conventional EM”. Granted that is true;
however, EM or perhaps other forms of microscopy could be used to locate particles, even within cells, and
then local fields could be
accuratley modeled around these particles based on the known physics of
superparamagnetic particles in the presence of a bias field. T2 relaxation could then be predicted in the
same way that the authors are doing here. So in other words, I think the autho
rs may be overstating the
importance of NV microscopy as a way of predicting T2 relaxation. I’d like the authors to discuss this, either
here or in Discussion or both.
Thank you for this suggestion. We have added a discussion of this topic on lines
171
-
18
3
, emphasizing
that while this study used particles with known properties in experimentally controlled scenarios to
validate
our method, th
e
tech
nique
we have developed
can be applied to magnetic field sources with unknown
properties, which would
not be po
ssible with electron microscopy or other localization methods that do not
directly measure magnetic fields.
Page 4 line 72: “after incubating them ...”
authors should provide data about the loaded cells, e.g. the
loading level in units of pgFe/cell, any
other characteristics of potential relevance and interest to readers
involved with cellular MRI.
Thank you. As suggest
ed
, w
e
have added data on the iron loading level in
(
pg/cell
), reported on lines 98
-
101
and
discussed in the methods on lines
285
-
295
.
We note that these
results match up
very
well with the
iron concentration predicted from
NV
magnetometry
, further validating the
accuracy
of our NV
data
fitting
procedures.
Page 4 line 79: “3D maps of magnetic field sources in the sample”
these maps should correspond to
maps of ION particle location / size, I believe, and could be validated using EM or other microscoyp of the
same samples / cells. I would like to see valida
tion of this type. Can authors do this and comment on this?
Thank you for this suggestion.
In order to provide
independent
confirmation of particle localization, we
fluorescently labeled the nanoparticles and performed
an additional
set of vector
magnetometry
experiments
together with direct fluorescent detection of the particles.
These results are provided in
S
upplement
ary Fig
.
8
and referenced in the main text on line
s
97 to 98
.
In brief, w
e found a strong
correspondence
between the (x,y)
localization of our fitting technique and the centroid of the fluorescent
signal from the magnetic cluster
s (with an
average offset
of
790 ±
105
n
m
)
.
We believe this modest offset
is due
to
physical deformation of the diamond and attached glass due to
heating by the laser
during NV
measurements
, and future work improving drift correction could help improve the fidelity between
fluorescence imaging and NV magnetic field source localization.
3D fluorescence localization is not possible
in our NV microscop
y setup
because it is not confocal
, and moving the samples to a confocal microscope
while keeping the precise field of view was not feasible. Likewise, it was not feasible to keep spatial
registration with thin
-
sectioned EM samples.
However, in addition to
this 2
-
D localization data, the accuracy
of our NV data fits is corroborated by independent measurements of average iron content, as discussed in
our response to the previous question.
Page 5 line 84: “Then, the off
-
diamond height (z) ...”
this seems lik
e a potentially very ill
-
posed problem.
Authors should show an analysis of this. For example, it sounds like it would be difficult to distinguish a
different size particle from a different z
-
height. If the ION cores are not monodisperse (and they usually
a
ren’t) then this seems like it could be a significant problem to me.
Thank you for this comment.
Although
this was
n
ot immediately intuitive
to us when we started the project
,
the problem of z
-
localization is, in
-
fact well
-
posed in the vast majority of scenarios. As clarified in the
revised
text on lines
316
to
319
, and demonstrated with a proof in the Supplement (equations
S5
to
S10
), the fact
that the magnetic field is measured at
multiple
points in the x
-
y plane
of the diamond, and that the impact
on this planar field pattern is affected differently by height and magnetization,
allows both the height off the
diamond and strength of
the field source to be estimated. As shown in the proof in SI,
there
does not
exis
t
a
pair of different
(M,z) value
s
such that the magnetic field is the same
for (M, z) and
(M’,z’) for all (x,y)
coordinates in the measurement plane.
A basic assumption of this model is that the sources can be
modeled
as point
-
like. For s
cenarios
including sparse particle labeling and
nanoparticle clusters
internalized by cells
,
this is justified. However, for more diffuse deposits of magnetic material,
a more refined fitting approach
may be required.
The need for
future work
in this direction
is
stated
in our
revised
Discussion
on lines
181
-
183
.
Page 5 line 98: “Importantly, since this information ...”
-
But is it possible to make NV measurements and
T2
measurements on the same sample? Also, how many cells (or what density of cells) can be measured
with the NV method?
Thank you for this question. Measuring the same exact sample with both NV magnetometry and MRI would
be very difficult with existing appar
atus.
Even if one could develop a method to section a biological specimen
corresponding to a single MRI voxel, the size of a
typical high resolution
voxel
has dimensions of (100 μm)
3
,
while the typical field of view and of NV magnetometry represent
s
a volu
me of ~ (20 μm x 20 μm x 10 μm)
.
For this reason, we believe the methodology presented in this study, which allows a biological specimen to
be sampled using NV magnetometry and used as input for predictive modeling of transverse relaxivity, is
important an
d advantageous for the task at hand. However, as it is now becoming possible using AC NV
magnetometry to measure nuclear spin precession, it is conceivable that future studies could measure both
the magnetic field and water relaxation in the same specimen.
This possibility is discussed in the revised
manuscript on lines
201
to
203
.
Page 5 line 101: What was a 1:1 mixture necessary and what would the consequences of using a different
mixture be?
We mixed the supplemented cells with unsupplemented
cells to maintain a measurable T2
in our MRI
scanner. Unmixed cells could be used if loaded with
other
magnetic sources. Other mixtures would be
expected to have predictable effects on T2.
We have added a comment
to this effect on line
s
113 to 114
of
the main text and lines
380
to
382
of the
methods section.
Page 5 line 104: “Monte Carlo prediction”
-
It is unlikely that cells are arranged in such a regular cartesian
grid of equal
-
sized spheres. Authors should comment on the changes in T2 that aris
e from irregular
distribution and size of cells.
Thank you. We agree that this
is a
significant
simplification
, which has nevertheless produced useful
predictions in other studies modeling MRI contrast
. We have added a
comment
on line
s 339 to 341
,
drawing
attention to
the simplification
and citing other papers in which
this or similar simplifications have
been used.
Page 5 line 106: “concentration of IONs”
-
However, T2 could have been predicted from knowledge of
particle location/size within a cell, which might for example be measurable by EM or other light microscopy.
The same Monte Carlo prediction of T2 could be d
one from this knowledge, which would therefore not
require NV microscopy. Authors need to justify why NV microscopy is necessary for understanding the
basics of T2 in ION
-
loaded cells.
Thank you. Please see our response to
the
question
regarding page 4 li
ne 79
, above, addressing this issue.
Page 5 line 110: Fig. 2f
the figure is labeled "clustered" but this is ambiguous. IONs could be clustered
extracellularly or could be confined / clustered inside sub
-
cellular compartments. I believe these two
situati
ons should yield different T2 values but the authors should comment. Also, how did their simulations
deal with the barriers / restrictions to water motion introduced by sub
-
cellular compartment membranes?
One relevant simulation that I’d like to see would
be to show simulated T2 values for extracellularly clustered
Fe particles, and to compare to intracellularly compartmentalized Fe particles.
Thank you for this insight.
To address this question, we have added 3 new simulations to the manuscript.
These simulations are described in detail in the
SI
, with their results potted in Supplementary Figure
7
.
They are also referenced in the main text on lines
123
to
125
.
Page 5 l
ine 118: “900nm”
why so large? Is NV measurement / microscopy not possible using more
conventional IONs? This is not a particle size that is commonly used for in vivo “clinical” applications of
IONs.
Thank you for this question. As we have clarified in the revised text on lines
131 to 132
, our goal in
administering these particles was to create a proof
-
of
-
concept scenario for punctate iron oxide deposits in
the liver rather than a clinical scenario inv
olving ION administration
for contrast imaging
. Using 900 nm
particles allowed us to obtain such punctate deposition while producing reasonable T2 contrast in MRI
.
In
addition, the detection of larger particles
with NV magnetometry
is more robust in our pr
oof
-
of
-
concept
experiments to issues such as imperfect flattening of histological samples against the diamond. The
optimization of
histological preparations
for future studies of smaller and biogenic field sources in tissues is
discussed on lines
191
to
19
6
.
Additionally,
we
cite
several major studies in which
micron
-
sized iron oxide
particles
were used as contrast sources in
in vivo MRI experiments
(line 190)
.
Page 5 line 123: “punctate”
doesn’t look punctate to me in Fig 3c. In fact
the images in Fig 3c are quite
poor
I don’t recognize structures in the fluorescent images (they are very poor quality) and don’t
understand what correlations I’m supposed to be making between the magnetic field maps and those
fluorescent images. Author
s need to improve image quality and make those correlations more clear.
We have clarified
in
the figure legend and accompanying text
(line
s
138
-
139
)
that the punctate feature
s
of
the iron
-
loaded liver images shown in the top part of Fig. 3c
(
and in the
additional tissue sections in
Supplementary Fig. 4
)
are the individual
magnetic dipole
s (
strong
local minima and maxima
next to each
other
)
observed in the NV image and the single fluorescent source observed in the fluorescence image.
By
comparison, no pun
ctate features are observed in the non
-
iron loaded control tissue.
Note that the non
-
uniform background in the NV image reflects the underling noise floor of the NV diamond measurement
,
likely due to higher
-
order strain effects.
S
ignal from
histological
samples
is weaker than in cultured cells
because
magnetic sources are offset
further
from the diamond surface. The saline magnetometry image
shows no significant magnetic field signal, showing only the background noise in the diamond. The top
fluorescent i
mage in
F
ig
.
3c shows a bright spot corresponding to the location of the nanoparticle cluster
,
while t
he lower fluorescent image just shows the background tissue autofluorescence
(which appears
bright
er than in the top image
because fluorescent images were
acquired with automatic gain).
Further
discussion of the fluorescent imaging of the tissue sections has been added to the figure caption and to the
m
ethods section (lines 409 to 412
)
,
Page 5 line 138: “This allowed us ...”
-
Similar to a comment above, why
is it not possible to perform source
localization in this situation
-
that would be more informative and would allow a more direct validation against
optical or EM, and more direct confirmation that "clustering" or sub
-
cellular compartmentalization is bei
ng
measured.
Thank you for this comment.
This limitation
stem from the fact that keeping cells alive
requires limiting the
light dose
applied to the specimen
, resulting in
a tradeoff
between SNR, temporal resolution and
the
number
of NV axes along which t
he magnetic field is measured.
For this proof
-
of
-
concept experiment in live cells,
we chose to increase temporal resolution
while
imaging the
magnetic field along a single NV axis
, which
allows dynamic imaging of cluster formation and movement within the c
ells, but not localization in 3
-
D
.
We
have added text on lines
153
to
156 to make this limitation explicit.
We believe
l
ive
-
cell vector magnetometry
is achievable
with
increased
SNR, which
is
within reach for future studies with improvement
s
described in
the discussion on lines
191
-
196
.
Page 5 line 145: Discussion
-
This Discussion is very brief. I would like to see more, such as a more detailed
discussion of limitations (such as the ill
-
posed nature of source localization and why source loc
alization
was not performed on the tissue samples), also comparison to any other technologies for microscopy of
magnetic fields such as microSQUID, discussion of sensitivity, spatial resolving power for sources, and
temporal resolution.
Thank you for this
suggestion. We have significantly expanded the discussion
, lines
167
-
203
,
in response
to this
comment and other questions and suggestions
from the referee.
Page 8 line 174: “unknown”
why is this not known? Seems like it would be important to know this
, to allow
others to replicate this work. Authors should clarify.
We have added this information to the text on lines
218
to
220
after getting it from the diamond
manufacturer.
Page 9 line 207: “sufficient out
-
of
-
plane field strength ...”
athors
should be more clear about what this
means
-
how much is "sufficient" and what are the specifications / tolerance limits for this bias field uniformity
or other characteristics.
Thank you.
We have
augmented
our explanation of this step in the methods
section
, lines
252
-
256
, to
specify why an out
-
of
-
plane field component was necessary
.
We have also clarified on lines
262
to
264
how any non
-
uniformity in the bias field is subtracted from magnetometry results, and
included
an estimate
of ou
r background bi
as field gradient
(based on a representative image)
.
Page 9 line 208: “ODMR”
this acronym has not been defined.
Thank you for pointing this out. The definition has been added
on lin
e
253
of the revised manuscript.
Page 9 line 215: “quadratic
background ...”
how is bias magnet inhomogeneity corrected for at the source
localization stage?
We have revised the text on lines
261
-
264
to clarify that i
nhomogeneities in the bias field are accounted for
prior to the source localization stage by subtra
cting out linear and quadratic gradients from the image
, which
works well because the
b
ias field
has a much lower
spatial frequency
than expected signals.
Page 9 line 221: “sensitivity”
how was this sensitivity determined? It is good to see this sensiti
vity
expressed in units of ION particles that can be detected at a given spacing off the diamond; however,
commonly used IONs have iron oxide cores of 3
-
5nm, not 200nm. Authors should express sensitivity in
units of these common IONs since that is where th
e general interest would lie. If this NV microscopy method
is not going not able to sense conventional 3
-
5nm ION cores, then this is a significant limitation that needs
to be discussed.
Sensitivity was determined by measuring the standard deviation of sequential images.
As the magnetic field
at a point scales linearly with the magnetic moment of the source and the magnetic moment scales with the
volume of the particle, the minimum particl
e size that our current apparatus could measure with confidence
10 μm
off of
the diamond surface
would be
92 nm.
At the diamond surface, this detection limit comes down
to 10 nm and is largely limited by the thickness of the NV layer.
We have extended our
discussion of
sensitivity on lines 184 to 196
.
Page 9 line
223: “200nm”
does this refer
to the iron core size? If so, that seems too large compared to
standard/practical IONs commonly used for cell tracking.
This does refer to the
total
iron core size.
(These particles are multi
-
core,
with the
individual core
size not
provided by the manufacturer
).
The nanoparticle size was chosen
to provide
good SNR from single
nanoparticle
s
anywhere inside of the cell
, while being within the range of particles used in
MRI cell labeling.
While USPIOs are
widely used
,
other studies have
relied on detection of
hundred
-
nm and
micron sized
IONS
.
We have discussed this point and added references
9
,
10
, and
11
to the text on lin
es
74
-
76
and
189
-
191.
Page 9 line 227: “the bias field was aligned ...”
not clear why this was done, and why the same method
as in the cellular imaging (with bias field parallel to plane of NV layer) could not be used.
Thank you.
This is discussed in our
response to the question above concerning Page 5, line 138.
Page 11 line 285: “12.9degC”
seems like a pretty cold temperature. Why was this particular temperature
used?
We have clarified on line
358
-
359
that t
his is the temperature in our magnet bore
,
and was chosen to
maintain a correspondence between modeling and experiments.
Page 11 line 285: should also specify intrcellular/extracellular volume fractions.
Thank you for pointing out this oversight. We have added the intracellular volume fraction
on
line
339
.
Page 11 line 288: should specify units of the bulk spin magnetization; the summation implies that this is
unitless but does that make sense?
Bulk Spin Magnetization is normalized to the magnetic moment of a single water molecule for arithmetic
convenience. We have added this to the text for clarity
on line
359
-
560
.
Page 12 line 294: “Data presented ...”
can the authors justify that these numbers in this sentence are
large enough?
Thank you for this question.
We
selected these number so that
the uncertainty in the mean value was lower
than the uncertainty in the mean of
the
experimental trials
to which these simulations were compared
.
We
have clarified this choice in the text on lines
368
-
369
.
Page 12 line 308: “multi
-
echo spin echo”
was th
is a CPMG sequence? Authors should be more clear.
Authors should comment on the fact that T2 measurements will depend on echo spacing in this kind of
measurement.
Yes
this
is a CPMG
sequence.
We have revised the text for clarity
on line
377
. The combined
effects of
echo spacing and spatial frequency of the T2 contrast agent are indeed highly relevant
, and we have
pointed this out on lines
347
to
348
.
Page 12 line 309: “T2 relaxation ...”
this seems to imply that the signal decay was not monoexponential.
Authors should clarify. Also, the same may have been true for the simulated NMR signal decay and should
be commented on also.
Thank you. Both our experiments and simulations
exhibited
monoexponential decay starting with the first
echo in the CPMG sequence
. As observed in previous studies, before the first echo a rapid unrefocusable
dephasing of spins in very close proximity to magnetic field sources causes additional relaxation that is not
part of the monoexponential fit.
Page 12 line 312: “unsupplemente
d ...”
were these live or fixed cells? If live cells, wouldn't the IONs have
been taken into the cells over time?
The cells were
live but were imaged immediately
after supplementation and were transported to the MRI
on
ice to
prevent
endocytosis. It is
also unlikely that the cells would actively endocytose during imaging
given the temperature in the magnet bore.
This has been clarified in the revised text on lines
394
-
395
.
Page 13 line 328: “to seal ...”
does this imply that a vacuum was used to force t
he tissue against the
diamond? If so, authors should be more clear.
Vacuum grease was used on the edge of the cover slip to hold the sample still and tight to the diamond.
No vacuum was used.
We have adjusted the text for
clarity
on line
s
407
-
408
.
Page
13 line 331: “single NV axis”
which axis specifically?
The NV defect exists in 4 distinct orientations in a tetrahedral configuration. We
probed
the axis
aligned
with the applied bias field.
We selected the bias field orientation based on convenience in
our apparatus,
but this choice is arbitrary.
Page 13 line 332: “This strong ...”
why wouldn't this strong bias field have been used for all experiments,
not just this one? Seems like it would be produce stronger fields and therefore better measurement
pr
ecision.
Thank you
for this question
. Our histological measurements were performed with the bias field aligned
along a single NV axis, and we collected data from only that axis.
This allowed us to boost the field strength
without producing off
-
axis fields deleterious to
NV fluorescence contrast
.
We could not use the same
approach for vector magnetometry, where bias field had on
-
axis and off
-
axis components for all four NV
axes and
could therefore not be too strong, as discussed in response to
an earlier question.
Page 18 figure 3 caption: “a, h and i”
I don’t see these labels.
Thank you for drawing this to our attention. The figure has been corrected.
Page 19 figure 4: Is it not possible to show optical (e.g. brightfield) images at all the same time points as
the magnetic field images? Authors should specify how large scale bars are.
We have
added
the bright field images from the long time
-
course stud
y
to the supplement
.
As the brightfield
lamp was adjusted before magnetometry commenced, there is a change in illumination for the later images.
The “fast” study did not allow sufficient time in
-
between scans for bright field imaging with our current setup
.
Thank you for pointing out the omission of the scale bar size. We have added this to the figure caption.
Page 19 figure 4 and associated text in the main body: Is it not possible to localize magnetization sources
in this situation of tissue sample (like
they did for cell samples?). If not, why not?
This question is addressed in our response to the question above concerning Page 5, line 138.
Thank you very much for your detailed and helpful feedback
.
Citations:
1.
Pfeuffer, J., Flögel, U., Dreher, W. & Leibfritz, D. Restricted diffusion and exchange of intracellular
water: theoretical modelling and diffusion time dependence of 1H NMR measurements on
perfused glial cells.
NMR in Biomedicine
11
, 19
-
31 (1998).
2.
Mukhe
rjee, A., Wu, D., Davis, H.C. & Shapiro, M.G. Non
-
invasive imaging using reporter genes
altering cellular water permeability.
Nature Communications
7
, 13891 (2016).
3.
Le Sage, D. et al. Optical magnetic imaging of living cells.
Nature
496
, 486
--
489 (2013)
.
4.
Glenn, D.R. et al. Single
-
cell magnetic imaging using a quantum diamond microscope.
Nat Meth
12
, 736
-
738 (2015).
5.
Steinert, S. et al. Magnetic spin imaging under ambient conditions with sub
-
cellular resolution.
4
,
1607 (2013).
6.
Hall, L.T. et al.
Monitoring ion
-
channel function in real time through quantum decoherence.
Proceedings of the National Academy of Sciences of the United States of America
107
, 18777
-
18782 (2010).
7.
I. Lovchinsky, A.O.S., 1, 2* E. Urbach, 1 N. P. de Leon, 1, 2† S. Choi, 1
K. De Greve, 1 R. Evans,
1 R. Gertner, 2 E. Bersin, 1 C. Müller, 3 L. McGuinness, 3 F. Jelezko, 3 R.. L. Walsworth,1,4,5 H.
Park,1,2,5, 6‡ M. D. Lukin1‡ Nuclear magnetic resonance detection and spectroscopy of single
proteins using quantum logic.
Science
3
51
, 836
-
842 (2016).
8.
Kucsko, G. et al. Nanometre
-
scale thermometry in a living cell.
Nature
500
, 54
-
58 (2013).
9.
McAteer, M.A. et al. In vivo magnetic resonance imaging of acute brain inflammation using
microparticles of iron oxide.
Nature Medicine
13
,
1253
-
1258 (2007).
10.
Shapiro, E.M. et al. MRI detection of single particles for cellular imaging.
Proceedings of the
National Academy of Sciences of the United States of America
101
, 10901
-
10906 (2004).
11.
Tarulli, E. et al. Effectiveness of micron
-
sized
superparamagnetic iron oxide particles as markers
for detection of migration of bone marrow
-
derived mesenchymal stromal cells in a stroke model.
Journal of Magnetic Resonance Imaging
37
, 1409
-
1418 (2013).
Reviewers' comments:
Reviewer #1 (Remarks to the Author):
The authors have sufficiently addressed my original comments. Having read the responses to the
other reviewers, I would like to point out that the typical high resolution for MRI cited to reviewer 3 of
100x100x100 μm is true for clinical MRI, but micro
-
MRI
, especially as performed in a vertical bore
magnet, may be capable of significantly higher resolution, on the order of the NV magnetometry
resolution.
With regards to the use of C PMG: it is important to only use even echoes. There is mention of the
"fir
st echo" in the response to reviewer comments.
Line 132: "efficient" iron loading, or "sufficient" iron loading.
Line 345: make explicit mention that inner
-
sphere effects can lead to additional dephasing that will
not be reversible by use o f typical C
PMG sequences (as they occur on a time
-
scale much faster than
180° refocusing pulses period)
Line 347
-
348: This sentence sounds awkward and poorly justified. The interecho spacing may indeed
affect T2 measurements in the case of chemical exchange (i.e.,
C arver
-
Richards model) or very large,
localized field gradients. It is not obvious to me that this was tested to see if it applies to the case at
hand, as only one tau_cp was used for modeling (5.5 ms). There is no citation to justify the "...affect
the ef
ficacy of the refocusing pulses..." sentence. Refocusing pulses don't care about tau_cp, they are
as efficient as they will be at 100 μs as they are at 100 ms. What matter is how well you can sample
the T2 decay. This sentence should be revised to read som
ething along the lines of "Adjusting the
C arr
-
Purcell time can affect the determination of T2".
Reviewer #3 (Remarks to the Author):
The revisions adequately address my original comments
.