Responding to More than a Response:
Tenotomy Improves INS Waveforms
L.F. DellÕOsso, Ph.D.
From the Daroff-DellÕOsso Ocular Motility Laboratory, Louis Stokes Cleveland DVA Medical Center and CASE Medical Center; and the Depts. of Neurology and Biomedical Engineering, Case Western Reserve University, Cleveland OH, USA
OMLAB Report #071107
Written: 7/9/07; Placed on Web Page: 7/11/07; Last Modified: 9/23/08
Downloaded from: OMLAB.ORG
Send questions,
comments, and suggestions to: lfd@case.edu
This work was supported in
part by the Office of Research and Development, Medical Research Service,
Department of Veterans Affairs.
Experience has taught me the damage that can be caused by
the publication of anything but the best information in the scientific
literature. That is the reason for peer review. Its purpose is to have items for publication pass the
careful scrutiny of experts in the field. Sometimes, the peer review process
fails; bad information enters the literature, where, even if later retracted,
it remains to cause its damage.
The situation that prompted this Report is neither a case
of different conclusions drawn by separate groups performing equally good
science nor anger over my conclusions being honestly questioned and criticized,
resulting in a fit of pique on my part.
When writing a Letter to
the Editor regarding a journal publication, one understands that the authors
will be given the opportunity to write a Response if they so choose; that is
fair. It is expected that their Response will be limited to the criticisms
contained in the original Letter; to prevent an unending chain of responses by
both parties, that is all that is permitted by the journal. Unfortunately, some
authors abuse their opportunity to respond to the scientific concerns of a
reader by: 1) not responding directly to the criticisms in the letter; 2)
introducing topics that are unrelated to the criticism; 3) withholding critical
information that is detrimental to their characterizations; 4) making arguments
based on false premises; 5) attacking the author of the Letter, or his work; or
6) combinations of the above. In this way, they hope to obfuscate the key
issues underlying the criticisms in the Letter, misdirect the reader, and cast
doubt on the source of the criticism. Web publication provides a mechanism for
the authors of the Letter to respond to such a Response, particularly when the
abuse is egregious.
The subjects of this report
are: 1) a pair of papers (companion papers) that attempted to assess the
effects of tenotomy on Infantile Nystagmus Syndrome (INS, aka CN for congenital
nystagmus) (1,2); 2) a Letter to the Editor (3); and 3) the Response by some of the
authors (4). The circumstances by which one of the
companion papersÕ authors approved the Letter, refused to
author the Response, and was also an author of a paper whose results
contradicted those of the companion papers are complex and involve
questionable behavior on the part of some of the companion papersÕ
authors; that is discussed in more detail elsewhere (5).
With
regard to the Response, my use of the term, ÒauthorsÓ refers to its three
signatories, Optican, Miura, and FitzGibbon. With regard to the companion
papers, for reasons that will become apparent (see below and elsewhere (5)), I also use the term, Òresponsible
authors;Ó here I am referring specifically to Optican and Miura who were
responsible for the data mining and analyses; based on my discussions with
Hertle, I do not include him. I have no direct knowledge of the extent of
FitzGibbonÕs involvement in the actual data analyses for the papers (by his
inclusion as a signatory to the Response, he appears to be willing to share the
responsibility for them). Also, the use of the pronoun ÒIÓ in the Response and
the irresponsible personal attacks it contains suggest that Optican was the
author and, as was done in the companion papers, other ÒauthorsÓ were added
later.
In my Letter to the Editor, I restricted my discussion to
the problems with the science of the companion papers. The key criticisms of the science were
not persuasively addressed in the reply by the responsible authors. I believe their reply misdirects and
obscures instead; that is bad science.
1. The wavelet
paper used a method that is neither the accepted standard nor was ever used, or
demonstrated to have the necessary sensitivity, to detect the changes in
foveation quality that the NAFX does. Therefore, the authorsÕ null finding
cannot be used, as they did in their abstract, to conclude that tenotomy had no
effect on the waveform.
2. Neither paper
used data from controlled fixation by the eye whose data were analyzed; the
authors chose not to analyze the 7 of 8 records from each recording session
that contained intervals of controlled fixation. Therefore, their analysis
included large eye deviations due to switches in the fixating eye and,
therefore, could not be used to detect any changes with a significant effect on
vision.
3. Neither paper
used artifact-free data. Therefore, the data analyzed included artifacts due to
blinks, voluntary saccades to other targets, and large involuntary drifting due
to inattention; these significantly reduced their signal-to-noise ratio and
further increased the likelihood that their methods would prove insensitive to
the tenotomy-induced waveform changes and precluded the conclusions in the
abstracts.
4. Neither paper
used properly calibrated data. Calibration consisted of using mean eye position
to get the eye within Ò10¡Ó of the target and it was presumed (incorrectly, as
I showed in my Letter) that the ÒpreferredÓ eye was always the fixating eye. (This methodological faux pas was not evident until the responsible
authorsÕ failure to accurately calibrate the data was inadvertently revealed in
their Response while attempting to justify their poor choice of which data
files to analyze.) Accurate analysis of waveform changes affecting acuity requires accurately calibrated data from the eye
that is actually fixating, not presumed to be fixating and certainly not 10¡ or
more from the target.
5. The wavelet
paper used data files that were mathematically pre-treated in a manner that
further increased their noise content. This had the effect of masking
significant changes in the waveforms and reduced their
averaged-wavelet-coefficient analysis to the equivalent of a Fourier spectrum.
Also, the pre-treatment method can only be used on stationary data; INS is not
stationary.
6. The dynamical
systems analysis paper was based on the presumption that INS was a
single-source oscillation. Decades of research indicate that the multiple types
of nystagmus in INS are due to two or three different kinds (read, underlying
mechanisms and anatomical sites) of oscillations generated in different ocular
motor subsystems. That precludes the conclusion in the abstract.
7. The companion
papers were written in a misleading manner, including selective referencing and
the omission of critical information.
1. The authors
did not address these key criticisms.
2. The authors
did not effectively address this key criticism. They falsely claimed that
artifacts could not be identified (see below).
3. The authors
did not address this key criticism.
4. The authors
indicated they could not accurately calibrate the data, but the significance of
ÒanalyzingÓ poorly calibrated data and making critical comparisons between such
ÒanalysesÓ was apparently not appreciated. The authors falsely claimed that
calibration was Òdifficult;Ó although it might have been difficult for them, it
was not for someone with experience in the recording, calibration, and analysis
of INS data (see below).
5. The authors
did not address these key criticisms.
6. The authors
did not address this key criticism.
7. The
prevalence of false and misleading statements and the authorsÕ failure to
include critical information in the Response was even worse than in the
Companion Papers.
Page 3095,
paragraph 1: Although the description of why Hertle did not sign their Response
seems to mirror the statement in my Letter, careful reading shows that it does
not. When given the opportunity to read, edit, and comment, Hertle agreed with
Òthe need for and contentÓ of my Letter but not of their Response. There is no
indication that he had any effect on the final content of the Response. Dr.
Hertle has read this Report and found it fair and factual (see Comment below).
Page 3095,
paragraphs 2 - 4: The NEI Clinical Trial was totally mischaracterized in
paragraph 2. The main outcome measure was the NAFX that specifically measures eye-movement
changes resulting from tenotomy; the vision measures were secondary. Thus, the approved NEI Clinical Trial
was specifically designed to measure Òchanges in the eye movements before and
after tenotomy as a clue to the mechanism underlying its therapeutic effects.Ó
In fact, I personally analyzed approximately 880 masked, eye-movement data
records over the course of the Trial. The unsupervised data mining of Optican
and Miura was neither needed nor approved by all of the members of the Clinical
Trial research team. When their early attempts to discredit the Clinical Trial
were detected in the middle of the Trial in violation of the NEI DSMC, they
were specifically forbidden to submit their data (5).
Their benign description in this paragraph of their ÒreasonableÓ efforts served
only to hide and justify their clandestine actions. False descriptions of the
Clinical Trial are repeated in both paragraphs 3 and 4, for exactly the same
reasons. In the Methods of the companion papers the following appears, ÒThe
protocol was approved by the NEI Investigational Review Board.Ó Lest anyone be
misled by the inclusion of that statement, the NEI IRB approval was for our
Clinical Trial; it was not
an approval of those two studies. Miura and Optican were not a part of the
Clinical Trial and conducted the companion studies without the knowledge or
approval of all of the scientists conducting the Clinical Trial.
Page 3095,
paragraphs 4 and 5: Their introduction and discussion of the proprioception
hypothesis for the mechanism underlying the INS waveform changes due to
tenotomy was a red herring. Our hypothesis neither invoked nor needed a
Òstretch reflex.Ó The ÒsmallÓ in Òsmall-signalÓ is with respect to saccades
(6);
therefore, INS slow phases are indeed, Òsmall.Ó BŸttner-EnneverÕs recent
discoveries of two types of ocular motor neurons (ÒfastÓ and ÒslowÓ) (7,8)
and GoldbergÕs finding that proprioceptive signals reach the monkey primary
somatosensory cortex (9)
provide both the anatomy and physiology to support our Òworking hypothesis;Ó
OpticanÕs diversionary arguments were mired in an old, and possibly incomplete,
paradigm that did not apply to our hypothesis.
Page 3096,
paragraph 1: The NAFX was designed to be applied to data from the fixating eye
during fixation of a target; to do otherwise, precludes its tight correlation
to visual acuity (10).
It has been repeatedly demonstrated by many users, in our lab and elsewhere, to
be both objective and the most sensitive measure of precisely those changes in
slow-phase waveforms that effect foveation (10-20).
All data were analyzed according to a strict paradigm, detailed in our Clinical
Trial protocol and approved by the NEI after a site visit to our lab. To state
otherwise and invoke false images of data selection and bias was nothing more
than a personal attack on the integrity of the method and those that developed
it. It was also predicated on the authorsÕ withholding critical information
from the reader in an attempt to justify their use of two apparently
insensitive methods. Specifically, the authors failed to inform the readers
that all of the NEI
Clinical Trial data analysis using the NAFX was done with masked data and redundant masked data files to both prevent
bias and demonstrate the
objectivity and repeatability of the NAFX. In contrast, Optican and
Miura used unmasked
data that they selected
from our 880 files; therein lays the only opportunity for Òoperator bias to
creep inÓ. The authorsÕ statement that, Òchanges in either the CN generator
(sic) or plant would be observable with our methodsÓ is unsupported by either
the companion papers (even if they had applied the methods correctly to viable
data) or any others published to date.
Page 3096,
paragraphs 2 and 3: Their comments after quoting my Letter may seem reasonable
but are irrelevant. Our hypothesis does not claim that proprioception is used
for on-line control of individual eye movements. We hypothesized that
proprioceptive information is used to set the operating point (read,
Òsmall-signalÓ gain) of the muscles. It is the resetting of that operating
point after tenotomy that results in a diminished response (eye oscillation)
despite an unchanged brain-stem signal (nystagmus slow phase). Apparently, the
authors did not fully understand our hypothesis.
Page 3096,
paragraph 4: The authors recognize the seriousness of my criticism that they
made an Òuninformed choice of data paradigm 8 for analysis,Ó and Òmade serious
methodological errors in the application of both types of analysis.Ó They also
recognized the implications of that statement. However, the authorsÕ
characterization of these methodological criticisms as Òad hominemÓ is unjustified
and the prelude to their attempt to characterize the companion papers as joint
study by the listed authors. I shall not use the word ÒcluelessÓ to describe
HertleÕs knowledge of what was being done, how it was being done, or when it
was being done; I prefer ÒpreoccupiedÓ (with the recruiting, screening, visual
function evaluating (pre- and post-tenotmy), and performing tenotomies on the
patients in the NEI Clinical Trial. A case could also be made for Òna•ve,Ó
given his relaxed, trusting, and honest approach to all. Again, I cannot
comment on FitzGibbonÕs personal contributions to the actual analysis of the
wavelet paper. However, given the knowledge I have (see (5)),
my position is very defensible. I presume the ÒweÓ in why they chose the data
they did, refers to the responsible authors; given that I trained Hertle and he
has extensive experience running his own eye-movement recording labs
specifically for INS patients, Hertle certainly knows how to accurately calibrate
INS data without ÒdifficultyÓ and was not involved in choosing the long,
uncontrolled data files. In our monocular calibration paradigms, ÒroughlyÓ
(i.e., 10¡) is simply unacceptable. Despite what the responsible authors
ÒneededÓ for their choices of analysis techniques, there simply is no such
thing as 10 minutes of uninterrupted fixation of an LED, not by INS patients,
not by normal humans, not even by trained, hungry monkeys. The authors
acknowledge that CN is non-stationary but their noise-producing,
pre-conditioning routines were only valid for stationary signals, one of the
methodological errors they failed to address in their Response.
Page 3096,
paragraphs 5 and 6: The authors failed to recognize that the representative
record I ÒchoseÓ in my Letter to illustrate their errors was one of those they
ÒchoseÓ to analyze in their paper; whether pre- or post-tenotomy is just
another irrelevant factoid to my and HertleÕs argument that such records are
unsuitable. Are the authors suggesting that post-tenotomy data did not contain
those artifacts? If so, that suggests tenotomy also eliminates blinks, periods
of inattention, switches in the fixating eye, or voluntary saccades to other
targets in the patientÕs visual field; that certainly would be impressive but
would only justify using such records for the post-tenotomy data. The authors
continue to miss the point. INS is extremely sensitive to all of the above
influences and, therefore, they must be controlled or any analysis will be so
confounded as to be useless; but that was exactly my criticism. Our paradigms
were carefully written and based on decades of experience first, to allow for
accurate monocular calibration of all the data and second, to ensure we were
only analyzing periods of fixation by the eye whose data we were analyzing.
Under those conditions, an increase in the NAFX translates directly into an
increase in visual acuity; no such correlation has ever been suggested for
wavelets. With regard to what I ÒclaimÓ is noise, I can only state that my
experience in recognizing all of the above artifacts and distinguishing them
from true fixation in an INS patient is highly transferable, as the many
post-docs, students, and visiting scientists who studied in our lab can attest;
the responsible authors have no comparable experience and to them, it appears
magical. They claim their methods required no subjective judgments of the kind
all researchers in ocular motility make to ensure they are analyzing clean
data; clearly what was required was the kind of scientific judgment that was
not apparent in their papers. The diversion on Òmental stateÓ is just that; we
routinely differentiate attentive fixational eye movements from different types
of artifact, all of which are easily detected from the data by the trained eye.
It was refreshing to see that they agreed on the importance of fixation attempt
(they have learned
something from my work); I would only point out again the extensive literature
already demonstrating that our objective methodology (the NAFX applied
according to our strict paradigm) accurately detects and measures foveation
quality from fixation intervals that correlates closely with visual acuity (10-20).
What they failed to recognize is that the ÒfutureÓ has been with us for over a
decade.
Page 3096,
paragraph 7: I have already listed the many methodological errors in the
companion papers specific to each method. The authorsÕ speculation that Òany
effects of tenotomy should have been apparent at some time scale or in some
part of the state-space trajectoryÓ is a supposition that has never been
demonstrated, neither by them nor others. The NAFX does detect and accurately
measure the very small changes in the duration of the foveation periods of the
INS waveforms (or the position or velocity SDÕs of foveation) that result in increased
visual acuity; no one has ever demonstrated that either of their methods are
capable of such sensitivity, even when applied to clean fixation data without
the methodological errors in the companion papers. One could argue that the INS
waveform changes produced by tenotomy (and measured by the NAFX) are Òonly a
quite small effectÓ especially if one did not understand the significance to
improved visual acuity of even a 10-30 msec increase in foveation time or a 20%
decrease in either the position or velocity SD of foveation. Perhaps that is
why these ÒsmallÓ but mighty changes appear to be undetectable by the global
measures used by the authors. Again, the authors try to mirror statements from
my Letter but donÕt quite make it. The ÒsourcesÓ (plural) of INS are not the
same as trying to detect a change in a mythical ÒmechanismÓ (singular).
Page 3097,
paragraph 1: Unfortunately, the only thing the companion papers do show is that
two untried (on pre- and post-tenotomy INS waveforms) methods that were never
demonstrated to be sensitive enough to detect the post-tenotomy changes
measured by the NAFX, did not detect those changes when they were applied to
poorly calibrated, uncontrolled, and artifact-ridden data after mathematically
incorrect, noise-inducing pre-treatment and wavelet-coefficient averaging. That
proved nothing about the effectiveness of tenotomy in improving INS waveforms.
Tenotomy does not cause some undefined (magic?) changes in the afferent visual
system. It is applied to the peripheral motor system and that is where it has
its direct effects. Our dramatic findings on a single canine of improved
post-tenotomy NAFX, were considered sufficient evidence by the NEI to conduct
the Clinical Trial; that attests to their therapeutic strength. The medical
goal of improving vision should not cloud the issue of how to best measure the
effects of an EOM surgery; the direct effects of tenotomy are motor and that is
why we designed the NEI Clinical Trial to measure the eye-movement changes as
the primary outcome
measure. To do as the
authors suggest and measure visual acuity (or other psychophysical measures of
visual function) as the primary outcome measure(s) of a muscle surgery is just
bad science; in the Clinical Trial, we measured visual function in several ways
as secondary outcome measures
and, thereby demonstrated again their correlation to the NAFX-measured waveform
improvements.
Page 3097,
paragraph 2: The authorsÕ gratuitous reference to the paper on the tenotomy
procedure applied to a monkey with Fusion Maldevelopment Nystagmus Syndrome
(FMNS, aka LMLN for latent/manifest latent nystagmus) without citing the Letter
to the Editor pointing out the latter diagnosis, was discussed in my Letter.
What is amazing is the authorsÕ statement in their Response that whether the
monkeys had FMNS (a diagnosis agreed to by Tychsen) or INS, two mechanistically
and clinically different disorders, is a minor point. We demonstrated
tenotomyÕs effects on INS waveforms, not FMNS. The waveform studied in the
monkeys was the low-amplitude, high-frequency pendular oscillation that is
sometimes seen in addition to either INS or FMNS in humans; its very different
characteristics than INS waveforms may make it less sensitive to the effects of
tenotomy. My colleagues have repeatedly demonstrated in numerous peer-reviewed
publications the objective evidence of tenotomyÕs INS waveform improvements. We
never claimed that those improvements occurred only in brief intervals of
attentive fixation effort; in fact they persist for as long as the patient
attentively fixates. Inattention can eventually lead to a cessation of the INS
waveform and an artificially high NAFX but such a measurement would not be
related to visual acuity; that is why the NAFX is only applied to fixation data.
The authorsÕ mistaken presumption of a brevity in tenotomyÕs effects reflects
their confusion between tenotomyÕs permanent improvements with our time-proven
experimental paradigms that ensure gathering as much fixation data at as many
gaze angles as possible, in as short a time as possible. When dealing with
young patients (unlike monkeys) we usually have only one opportunity to get the
childÕs data and, because we are dealing with a low attention span and lack of
desire to be there constrained to look at boring LEDÕs, we only present targets
for enough time to ensure target foveation for a few seconds at a time (we then
repeat the stimuli). Thus, contrary to the false suggestion that we pick the
intervals to analyze, we actually use all the fixation intervals that the data files contain. It
should be noted that this mimics normal visual behavior where one looks at a
target, quickly identifies it, and then looks at another; e.g., ÒtargetÓ may
refer to different features on someoneÕs face. NAFX analyses on longer
intervals (10-30 sec without blinks or other artifact) taken from dedicated
adult volunteers yield exactly the same accurate measures of foveation quality
as those from shorter intervals.
Page 3097,
paragraphs 3-4: This attack on a pioneering and revolutionary body of work
involving this author with other respected scientists (including Hertle) in the
study of the ocular motility of the first mammals with achiasma (12,21-30)
is but an extension of the authorsÕ biased attempts to discredit the source of
the methodological criticisms of their companion papers contained in my Letter.
It is replete with the same kind of false statements, mischaracterizations, and
refusal to admit the obvious. All who were involved in the studies, who ever
saw the dog pre- and post-tenotomy, and the scientific community who read our
papers recognized the significance of the work. Tenotomy totally damped
(horizontal INS) or eliminated (vertical SSN) the nystagmus and radically
improved the dogÕs visual behavior; the impressive NAFX improvements merely put
an objective number to the obvious success of tenotomy. I will not dignify
their diversionary attack on the integrity of that body of work with a
point-by-point discussion of their misstatements as I have done with the rest
of their Response. If they disagreed with the findings of any one of those
papers, they should have written a Letter to the Editor, as I did. Unlike the authors
of the Response, my Response to such a Letter would have been confined to their
specific criticism. Regarding their comments on the data shown in a paper, all
papers can only show a representative subset of the data; their vacuous
statement is not valid criticism. INS waveforms show idiosyncratic variability
pre- and post-therapy; the important measure is in both the range of and
average value of key measures. In both, the NAFX shows post-tenotomy
improvements. In our experience, our paradigms show no significant variability
in the NAFX across patient visits; the number of return visits in the Clinical
Trial conformed to the NEI protocol and were sufficient to confirm what we
already knew from our years of experience.
Page 3097,
paragraph 5: Perhaps these authors donÕt know why visual function improves
post-tenotomy but our published data prove that it is the foveation
improvements in the INS waveforms that result in improved visual function,
including in patients with significant afferent visual deficits (10-15,17-20).
As to the etiology of INS, there is an excellent behavioral ocular motor system
model whose hypothetical causal mechanism for most INS waveforms has been
supported by its subsequent emergent predictive responses (31-33).
The rest of this paragraph is simply random speculation caused by their failure
or unwillingness to objectively evaluate the NAFX results.
Page 3097,
paragraph 6 (onto Page 3098): The demonstrated improvements in visual function
brought about by tenotomy are not Òclaims,Ó they are measurable facts already
proven to objective minds. These authors are not in a position to determine how
INS affects an individual (something about which I have direct knowledge) or
what therapeutic measures should be taken to greatly improve visual function;
that is a clinical opinion. The responsible authors do not have, to my
knowledge, the training or experience to offer this opinion. I know they lack
my training and experience in the study of INS waveforms. The responsible
authors are casting aspersions on results drawn from data that were properly
obtained, correctly calibrated, and analyzed (while masked) with objectively
proven methods; they did none of these things.
The Response failed to adequately respond to the important
scientific criticisms in the Letter. Instead, it was written in a manner both
to confuse and mislead the readers and used as a platform for a personal attack
(dressed up to look like ÒscienceÓ) on the author of the Letter. The
responsible authors revealed both a single-minded bias and a remarkable
ignorance of the past 45 years of INS research, beginning with, but not limited
to, the ability to accurately calibrate nystagmus patientsÕ eye movements. Bad
science can appear in good journals both in the form of papers and ÒResponsesÓ
to legitimate criticism, in this case, both. The false conclusions in their
abstracts remain unsupported by their own analyses. Tenotomy produces
significant improvements in INS waveforms that can be measured by the NAFX and
that result in improved visual function.
Acknowledgements
The author acknowledges the
contributions of the three Reviewers who helped ensure the veracity of the
facts presented herein.
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Although the information
contained in this paper and its downloading are free, please acknowledge its
source by citing the paper as follows:
DellÕOsso, L.F.:
Responding to More than a Response: Tenotomy Improves INS Waveforms. OMLAB
Report #071107,
1-12, 2007. http://www.omlab.org/Teaching/teaching.html
Note: This report was originally numbered as #070907
(date written) and was corrected to #071107 (date posted) on February 7, 2008.
Comment:
ÒYou have a done an excellent job being fair and factual, I have no problem with the text.Ó Richard Hertle, 7/9/07.
Addendum (added 9/23/08):
Able et al. published a paper that demonstrated the
inability of wavelet analysis (even when done correctly) to differentiate pre-
and post-therapy INS waveforms; wavelet analysis could not even differentiate
classical INS waveforms with very poor foveation quality from those with very
good foveation quality. The NAFX easily measures and differentiates all
nystagmus waveforms with differing foveation qualities. Thus, this paper
demonstrated conclusively that: 1) wavelet analysis of INS waveforms is too
insensitive to detect the visual-function improvements in foveation-period
characteristics, produced by the tenotomy and reattachment procedure and 2) the
NAFX does measure those waveform changes.
Abel, L.A., Wang, Z.I. and
DellÕOsso, L.F.: Wavelet Analysis in Infantile Nystagmus Syndrome: Limitations
and Abilities. Invest. Ophthalmol. Vis. Sci. 49:3413-3423, 2008. Apr 30 [Epub
ahead of print] PMID: 184505850