Randomised trial of acupuncture compared with conventional massage and “sham” laser acupuncture for treatment of chronic neck painCommentary: Controls for acupuncture—can we finally see the light?
BMJ 2001; 322 doi: https://doi.org/10.1136/bmj.322.7302.1574 (Published 30 June 2001) Cite this as: BMJ 2001;322:1574
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Sir,
We have read with interest the discussion of the recent paper by
Irnich et al 1 and their thoughtful reply. Dr Irnich suggests that some of
the criticisms are due to detail omitted from the paper because of space
restrictions, and we agree that this is an important issue. We are not
sure, however, if this argument can also be used for the ‘electronic’
version of the BMJ, as clearly much more detail is given here. Perhaps the
BMJ editor or the paper's authors could clarify this for us?
Even though Irnich et al's paper is far from perfect, we believe it
is an important study. We have no doubt that it will score highly on the
Jadad scale, but this is simply a measure of bias and not a reflection of
the quality of a trial per se. Scientific progress is generally a slow
process which is partially dependent on peer review, and it is vital that
we are able to learn from each other's constructive criticisms. We must
assure Dr Irnich that our comments were made in an attempt to further the
process of constructive scientific discussion after thoughtful
consideration.
With regard to Dr Irnich's comments on placebo, in particular the
needle developed by Streitberger 2 which Irnich felt was not a real
placebo because it could not be applied double blind. The definition of a
placebo is that it is inactive, harmless and given "to please the patient"
3 i.e. that it has no specific therapeutic effect 4. The fact that the
practitioner cannot be blinded during its use is an issue relating to
bias, not whether the Streitberger needle is a placebo. A single blind,
placebo controlled trial would conventionally require that the patient is
unable to detect the difference between verum and placebo. We feel,
therefore, that Dr Irnich may be a little premature in his castigation of
this needle, particularly in the light of Streitberger’s early results.
Whether the Streitberger needle is truly physiologically inert requires
further investigation. We feel, however, that the use of this needle is
not very far removed from the reality of acupuncture practice, and
probably represents one of the better options that we have at this present
time, although its use may be limited by the fact that it cannot be
applied to all acupuncture points. In our trials thus far, we have found
the technique can be performed easily and convincingly.
With regard to the outcomes used, we have not suggested that visual
analogue scales (VAS) are not valid in their own right. Our concern is
centred around the issue of how this was conducted. Combining VAS with
range of movement in this way, creates a new, previously unvalidated,
process of outcome measurement. We feel that it is scientifically
legitimate to question the validity of the outcome process for the reasons
stated in our original letter. Whilst Dr Irnich has answered some of the
questions we have raised in this regard, there was not a sufficient
description of this in the published methodology or the subsequent
correspondence. Questioning the validity of the primary outcome does not
in any way preclude us from commenting on the overall results of the study
as presented by the authors. The results clearly suggest that acupuncture
treatment was not superior to the ‘placebo’ control, and we therefore feel
justified in concluding that this trial was negative for acupuncture,
given those results.
We feel that details of the intervention should be clear in the study
methodology and that it is unacceptable to bury this within the reference
section. Reproducibility must be a prerequisite for any controlled trial.
The quality of scientific reporting within the field of acupuncture has
improved significantly over the last 20 years, both in our own and other
studies. Our quoted research relates to the process of outcome
measurement, not our inadequate reporting of treatment protocols over 15
years ago. We also fail to see why it might be ethically acceptable to
use a placebo treatment for five sessions but not for six or eight.
Surely an intervention is either ethically acceptable or it is not.
Lastly, with regard to the sham laser, we do accept Dr Irnich’s
statement that “there is always a first time”, although it is perhaps a
shame that such a large and important study has utilised a previously
unevaluated control. We would have expected some appropriate and
published pilot work prior to such a large scale study.
In conclusion we feel that this study would be difficult, if not
impossible, to reproduce from the information that we currently have
available to us. We are also unsure of the robustness of the outcome
measures and the placebo employed, and are therefore unclear how much
value we should place on the study's conclusions.
Reference List
1. Irnich D, Behrens N, Molzen H, Konig A, Gleditsch K, Krauss M et
al. Randomised trial of acupuncture compared with conventional massage and
sham laser acupuncture for treatment of chronic neck pain. British Medical
Journal 2001;322:1574-7.
2. Streitberger K,.Kleinhenz J. Introducing a placebo needle into
acupuncture research. Lancet 1998; 352:364-5.
3. Webster's Dictionary. The new international Websters dictionary
of the English language. Florida: Trident Press International, 1995.
4. Lynoe N. Is the Effect of Alternative Medical Treatment Only a
Placebo Effect. Scand J.Soc.Med. 1999;18:149-53.
Competing interests: No competing interests
Sir
We appreciate very much the opportunity to discuss by electronic
letters on the BMJ web site. When we analysed the results of our trial [1]
we were aware that they would be subject to a controversial discussion.
This was foreshadowed in the comment by Mike Cummings [2].
We agree that the results of our trial may be interpreted in different
ways, but we are surprised that the statistical approach and the study
methodology have been criticised.
Analysing the comments we believe that some points of criticisms are due
to superficial reading of the paper, while others are due to details
omitted from the paper because of space restrictions. In the latter case
missing details should not be interpreted in a negative way. It would be
preferable to contact the authors before commenting on unknown details.
Our reply in detail:
To Dr. Cummings:
Thanks to Dr. Cummings for his excellent comment on our trial, which
foreshadowed the current discussion. But there is one point we would like
to comment on. Many people in the field consider the placebo needle
introduced by our friend Konrad Streitberger [3] and similar approaches
like the Park Needle [4] as a real placebo. We do not think that it is.
It cannot be applied double-blind, that means it is not a real placebo
according to the requirements of a placebo in clinical trials. It
irritates the skin, it is a very artificial procedure far from the reality
of acupuncture practice, and stimulation techniques cannot be performed
adequately through a tube and a plaster in the real acupuncture group.
Konrad`s idea was a very good one, but it was not an appropriate placebo
for our study.
To Dr. Zarkovic:
Dr. Zarkovic addresses the main problem. He states that an alternative
conclusion might be possible because acupuncture is not significantly
superior to sham laser acupuncture in the main outcome measure. The
significant difference between acupuncture and massage might be explained
by harmful effects of massage.
This is not to be rejected a priori and we discussed this conclusion
extensively in the study committee. We rejected this conclusion for
different reasons:
1. The main outcome measure was improved by more than 50% compared to
baseline in 57% of patients who received acupuncture, compared with 32% of
patients who received sham laser and 25 % of patients who received massage
(Chi-square test: p=0.008).
2. There are clinically relevant improvements in the acupuncture group for
all outcome measures one week after treatment.
3. Acupuncture vs. sham laser: Regarding the main outcome measure there is
a clinically relevant difference, at least in the subgroup of patients
with myofascial pain and patients with pain for longer than 5 years.
Regarding secondary outcome measures one week after treatment, acupuncture
showed clinically relevant improvements in "range of motion" and "pain
related to direction" compared to sham laser (p-values just over 0.1) and
statistically significant differences compared to sham laser in two of
three verbal rating scales (p<_0.05. br="br"/>4. Acupuncture vs. massage: Acupuncture was clearly more effective than
massage. We do not believe that massage is harmful, because there is no
scientific evidence which supports this hypothesis [5,6]. Analysing the
results of the three verbal rating scales one week after treatment it is
shown in our paper that between 50 and 60 % of patients scored themselves
as improved. The large majority of the other patients scored no changes,
only 1.7% (global complaints, pain related to motion) or 3.6% (spontaneous
pain) scored themselves to be worse after massage (data not published).
Therefore we think that conventional massage (without special techniques)
as tested in our trial, even if applied by experienced therapists, is not
effective in the treatment of chronic neck pain. Hence, massage does not
appear to affect the natural course of disease.
We agree with Dr. Zarkovic that "positive thinking" in the medical
literature is a problem. We discussed clearly the limitations of our
study, and do not feel concerned by this.
To Dr. Ewing:
The answer may be similar to the reply to Dr. Zarkovic, but Dr. Ewing also
mentioned that efficacy means "better than placebo". This is appropriate
for drug therapy which can be evaluated by comparison with inert placebo
pills.
But how should we proceed in evaluating therapies, which cannot be
controlled by placebo, because a real placebo does not exist?
We need to remember, that a real placebo in clinical trials has to be
physiologically inert and needs to be applicable double-blind. Thus, there
is no real placebo which can be used in acupuncture research, and also in
many, many other therapies (physiotherapy, physical therapies,
psychotherapy, patient education, surgery and so on). Hence, in all these
therapies we will never be able to prove efficacy by clinical trials, and
it is always easy to argue that differences to any sham procedure are due
to an enhanced placebo effect.
Dr. Ewing stated that differences between therapies might be due to a
hierarchy of impressiveness of suggestions for each therapy, but
suggestibility seems not to be a major factor in modifying the power of a
placebo [7]. However, patients` expectations of treatment effects clearly
influence their responses [8].
We do not believe that patients expectations influenced our results,
because the credibility assessment of treatments did not show differences
between the three groups before and during treatment. The only exception
was a small difference after treatment between therapies which went in the
same direction as outcome measures, indicating an influence of achieved
effects for each group. But even after treatment there was a relatively
high credibility for sham laser and massage. (Data have been presented to
the reviewers and editors).
The effects of placebos in pain research are complex and they are
influenced by many known and unknown factors. Dr. Ewing cites some of the
most interesting studies.
It is a fact that we do not understand in detail how placebos work, we do
not even know if it exists [9].
To explain our results by stating that acupuncture in our trial is a very
good placebo, which works better than an established treatment or a sham
procedure with similar credibility, does not challenge our conclusion.
To conclude that acupuncture is not effective regarding the clinically
relevant effects we observed in patient with a long history is not
justifiable.
To Dr. Rifkin:
In our view Dr. Rifkin has confused our conclusion from the clinical trial
with the explanation for the observed effects. These are two different
things. How we came to our conclusion is shown in the above statements.
But to explain the results the mechanisms which leads to the results is
another thing. It may be that our explanation is not correct, we can only
discuss what seems to be most likely. We palpated for diagnostic reasons,
this is a form of counter irritation which can have physiological effects
[10,11]. Apart from this there might be other explanations e.g.
stimulation of acupuncture points by red light, or acupressure like-
effects, which we cannot prove.
We think you would agree that it is difficult to explain how placebo works
in detail and why sometimes there are strong effects and sometimes only
small?
Regarding the statistical analysis, we have not included in the tables the
p-value for the overall test in the analysis of variance including all
three treatments. This test should show statistical significance before
proceeding to pairwise comparisons, if the overall significance level
should be less than or equal to 0.05 for one hypothesis. For the main
outcome measure, the overall test resulted in a p-value of 0.0104 for all
patients, p=0.0027 for the subgroup with myofascial pain syndrome and
p=0.0265 for the subgroup with pain > 5 years.
The last point of criticism from Dr. Rifkin is unnecessary, since
Dunnetts´s test includes the adjustment for multiple comparison.
To Dr. Lewith and Mr. White:
We have great respect for the methodological work completed by Dr. Lewith
and his group in recent years. Therefore we are surprised about their
judgement of our trial methodology and we do not find objective reasons
for this.
Our study has undergone an extensive review process by the BMJ. It has
been reviewed by an internationally renowned specialist in clinical trial
methodology and by a statistician. The study design has also been examined
by international reviewers as part of a tender for research sponsorship
from the German Ministry for Education and Research (BMBF, formerly BMFT)
and was found to be worthy of sponsorship. In contrast to previous
studies, our bi-center trial is characterised by a large sample size,
adequate outcome measures evaluated by blinded observers, blinded
patients, sham control and alternative treatment control, individual
acupuncture treatment by more than one licensed acupuncturist, data
analyses performed by an independent institution, follow-up assessments
and documentation of drop-outs and adverse events. Taken together it will
score highly on the well-known scales assessing the methodological quality
of clinical trials (e.g. Jadad Scale, Oxford Pain Validity Scale).
It is said that our study is negative for acupuncture. We do not accept
this interpretation (see reply to Dr. Zarkovic, Dr. Ewing and Dr. Rifkin).
Furthermore, the arguments of Lewith and White are contradictory: They say
that the main outcome measure is not valid, but they accept it to say that
the result of the trial is negative. They should be logical: If an outcome
measure is not valid than the result is not valid !
In detail:
1. They argue that the treatments groups are inadequately balanced with
respect to myofascial pain syndrome and say that acupuncture may be
particular effective in this syndrome. This is what we have shown by
subgroup analyses !
2. They claim that they have too little information about the acupuncture
and massage treatments to be able to reproduce this study accurately. It
is true that in most of the acupuncture studies the form of acupuncture
used is not adequately described, but space restrictions on the
description of details in reporting clinical trials are well-known.
Therefore we proposed another procedure [12], which we carried out in our
trial: The detailed description of the acupuncture used in the trial was
intentionally disclosed in a publication subject to peer-review before the
results were published, in order to give readers, reviewers and
researchers the opportunity to better understand and review the
acupuncture used in the study. There is a reference in the paper! Massage
is adequately described as we named the techniques used by the therapists
and a citation is also provided allowing the reader to look up what these
techniques are in detail.
3. We agree with M. Cummings, who suggested that sham laser was a "good
choice". Lewith and White claim "that this is not substantiated by any
evidence in other studies". This is not possible because in this context
it is a newly introduced control group. There is always a first time ! And
our control treatments were equally credible. But we will soon supply
further evidence for the credibility of sham laser, because this was the
case in other acupuncture trials we performed and which will be published
soon. We agree with Lewith and White that "the choice of placebos/controls
in acupuncture trials is a vexed and probably unresolvable issue."
Therefore we discussed the limitations of sham laser as placebo in the
paper.
4. Lewith and White complained that we used the term "patients` beliefs"
to describe the credibility assessment and that the scale we used was
originally described by Borkovec and Nau. This is right, but we cited
Vincent because he assessed the internal consistency and test-retest
reliability of the scale [13]. The word "credibility assessment" was
replaced by "patients` beliefs" when the BMJ edited the text to make it
better understandable for non-specialists. Even if "patients` beliefs in
treatments" and patients` opinion on the "credibility of treatments" are
not a long way away from each other, their remark is correct, and we
should have used "credibility assessment".
5. Lewith and White said that "the treatment was limited to five
treatments, possibly too little for effective treatment". We have shown
that five treatments can be effective. However, the number of treatments
is an important limitation, especially with regard to long term effects,
as we discussed in the paper. There were ethical reasons not to treat
patients more than five times with a sham procedure.
6. Regarding the time points of assessments it is true that we did not
assess continuously, but we assessed five times during and after
treatment. This should be enough to gain valid results. They say our
strategy is unusual in a study involving acupuncture and chronic pain and
they give as reference two of their own clinical trials dating more than
15 years [14,15], which were performed on other conditions and which have
been judged to be of low or moderate quality in a recent review [16].
7. The main outcome measure was criticised by Lewith and White. They pose
questions about the procedure, then they give their own answers and
conclude that the outcome measure is not valid. We would prefer to provide
our own answers. The out come measure is validated - it is the visual
analogue scale to assess pain intensity ! The assessment was standardised
for procedures and even for day of time.
We are looking forward to the results which Dr. Lewith plans to
present later this year when his neck pain study is completed, and we do
not wish him a similar superficial comment which does not respect the fair
-play necessary for a scientific discussion.
To Dr. Morell and Mr. Wentz:
We do not comment on this discussion, because it does not concern our
trial, but we agree with Dr. Morell`s general characterisation of self-
referencing.
To Dr. Gunn:
We appreciate the work of Dr. Gunn, and we have invited him several times
to Germany to demonstrate his technique of IMS. We call the technique of
treating myofascial triggerpoints "dry needling" because this name is more
widespread. It can also be seen as a form of acupuncture at so-called "Ah-
Shi" points. We used this technique in combination with classical points
chosen according to the rules of TCM and ear points. By the way, some
meridians seem to be zones of referred pain pattern. We agree that the
diagnosis of myofascial pain syndrome and myofascial triggerpoints
requires experience. This was the case in our trial concerning both
independent examiners and acupuncturists. Teaching of acupuncture in
Germany includes the diagnosis and adequate treatment of myofascial
triggerpoints. This does not mean that traditional rules are unnecessary,
and we will soon publish a trial comparing immediate effects of dry
needling compared to distant acupuncture points and sham in chronic neck
pain. The data will show that distant points are also very important to
achieve beneficial effects.
To Dr. Lewis:
For the analyses the subjects were analysed by the groups to which they
were randomly assigned with all available information for each parameter
(no missing value imputation). All enrolled patients in this study were
treated as randomized, i.e., all actually received the correct treatment
(if treated). The number of patients in the tables reflect the patients
with available data for the analysed parameters, i.e., patients with
missing values for the outcome measures were not considered. This is the
reason for the differences between the numbers in the Figure and the
number in the Tables.
With kind regards
Dr. D. Irnich
Dr. A. Beyer
Department of Anaesthesiology,
University of Munich, Germany
M. Krauss, Dipl. Stat.
Biometric Centre for Therapeutic Studies,
Munich, Germany
Dr. N. Behrens
Dr. P. Schöps
Formerly: Department of Physical Medicine and Rehabilitation,
University of Munich, Germany
Dr. A. König
Department of Orthopedics,
University of Würzburg, Germany
Dr. H. Molzen
Dr. M. Natalis
Formerly: Department of Orthopedics,
University of Würzburg, Germany
Reference List
1. Irnich D, Behrens N, Molzen H, et al. Randomised trial of
acupuncture compared with conventional massage and "sham" laser
acupuncture for treatment of chronic neck pain. BMJ. 2001;322:1574-1577.
2. Cummings M. Commentary: Controls for acupuncture-can we finally see
light? BMJ 2001;322:1578.
3. Streitberger K, Kleinhenz J. Introducing a placebo needle into
acupuncture research. Lancet 1998;352/9125:-365
4. Park J, White A, Lee H, Ernst E. Development of a new sham needle.
Acupunct Med 1999;17/2:-112
5. Aker PD, Gross AR, Goldsmith CH, Peloso P. Conservative management of
mechanical neck pain: Systematic overview and meta-analysis. BMJ.
1996;313/7068:-1296
6. Braverman DL, Schulman RA. Massage techniques in rehabilitation
medicine. Phys Med Rehabil Clin N Am. 1999;10:631-49
7. Evans FJ. Expectancy, therapeutic instructions and the placebo
response. In: White L, Tursky B, Schwartz G. Placebo-Theory and Research.
New York, Guilford Press, 1985:215-228.
8. Turner JA, Deyo RA, Loeser JD, Von Korff M, Fordyce WE. The importance
of placebo effects in pain treatment and research. JAMA 1994;271/20:1609-
1614.
9. Hrobjartsson A, Gotzsche PC. Is the placebo powerless? An analysis of
clinical trials comparing placebo with no treatment. N Engl J Med
2001;344:1594-1602.
10. Willer JC, Roby A, Le BD. Psychophysical and electrophysiological
approaches to the pain-relieving effects of heterotopic nociceptive
stimuli. Brain 1984;107:1095-1112.
11. Sandkühler J. The organization and function of endogenous
antinociceptive systems. Prog Neurobiol 1996;50/1:-81
12. Irnich D. Demands, possibilities and limits of evidence-based
evaluation in acupuncture. Dtsch Z Akupunkt 2000;43:117-125.
13. Vincent C. Credibility assessment in trials of acupuncture.
Complement Med Res 1990;4/1:8-11.
14. Dowson DI, Lewith GT, Machin D. The effects of acupuncture versus
placebo in the treatment of headache. Pain 1985;21:35-42.
15. Lewith GT, Field J, Machin D. Acupuncture compared with placebo in
post-herpetic pain. Pain 1983;17:361-368.
16. Ezzo J, Berman B, Hadhazy VA, Jadad AR, Lao L, Singh BB. Is
acupuncture effective for the treatment of chronic pain? A systematic
review. Pain 2000;86/3:217-225.
Competing interests: No competing interests
Sir,
I do not intend to continue the debate with Paul Morrell about proper
use of citation frequency calculations, but should like to point out that
I am just plain 'Mr.'.
With kind regards
Reinhard Wentz
Competing interests: No competing interests
Sir,
It is a great pity that Dr Wentz [1] seeks to personalise an issue,
which is mostly of general importance. I can assure him that I have no
personal stake in whether the point of view I expressed was right or
wrong. My life does not depend upon it and I am not especially bothered
either way; I merely pointed to what seems like a genuine pattern [2]. I
also know I am not alone in forming this impression of this field. I am
sure those who wish to make such a trend disappear, will have their say,
whether they give their reasons or not, buried under a welter of
obfuscating figures, or otherwise.
"Dr Lewith is one of the authors of at least 70 papers published
between 1981-2001. He is the first author of some 50 papers, twelve of
which cite more than ten papers (range 11-115). In these papers he cites
himself on average 2.25 times (range 0-5) which suggests a mean self-
citation rate of 4.8%." [1]
If Dr Wentz can provide the data upon which he bases this reduced
global average of self-citation for Dr Lewith, which I believe has not
been calculated correctly, then I will reconsider the points I have made.
Clearly, in order to reduce a global average from 15.6% to 4.8%, a large
number of very small figures must have gone into the mix, especially if,
as in this case, the range extends upwards to 40%. As I do not believe the
sample I used was very untypical, being randomly and un-prejudicially
selected, I find it hard to believe Wentz’s low figures. He should list as
‘one’ - as I did - every time the name Lewith appears as an author in an
article cited, regardless of how many co-authors there are. He should
indicate the total number of references cited in ALL the 70 articles he
mentions [not just a selection] and the number of those that contain the
name Lewith as a co-author. Then convert that into an average percentage.
I think if he does that, the average will be higher than 4.8%.
At no point did I claim that Dr Lewith had done what he does
deliberately. It must be very easy to quote yourself all the time, without
even realising it. But it is a sloppy practice. To demand apologies is
therefore decidedly premature and would of course require that a
deliberate error of fact or interpretation had been made, from my side,
compounded no doubt with malicious intent. As no such requirements apply
in my case, I do not therefore see much reason to offer an apology.
Indeed, if anyone should be condemned to stumble forwards armed with
apologies then we might look instead to those who use this loathsome self-
citation habit so liberally in their publications.
Of course self-citation rates of 40-70% deserve to be denounced as
unjustifiable and disreputable, and I am astonished that Dr Wentz is so
reluctant to condemn the practice himself. If we also include regular
citation of a small coterie of co-workers, then he can rest assured, these
figures would be even higher. I did not actually use Dr Wentz’s word
‘ethical’; in fact, the word I used was 'respectable' and I see no need to
apologise for questioning how a 40% self-citation rate can attract much
respect. Indeed, as I previously indicated, 15.6% is still on the high
side. If I now introduce the word 'decent', I would say that as a rule-of
-thumb 'below 10%' is a 'decent' average self-citation rate, that is 1 in
10 listed references. 5% is better, but I would accept 1 in 10 as quite
'decent'.
Certainly, high self-citation rates are flagrantly unethical and it
is worth readers briefly contemplating why that is. The basis for anyone
using references in their work is to use the pooled resources of the
academic community to buttress their views, research methods, and to
interpret their findings, measured, as they so often are, against what
their predecessors have found. This is the established basis for article
writers quoting the works of others. It shows that one has read all the
most relevant literature preceding one’s work and digested its merits.
To which I would also add the following very wise sentiment: "the
urge to ensure the survival of a point of view with which an academic has
become identified is often a stronger driving force leading to bias than
is any possible financial gain or loss." [3]. Self-referencing looks
uncannily like a subtle means to ensure "the survival of a point of view
with which an academic has become identified." I would therefore say that
a more scrupulously balanced use of citations is an important way to avoid
accusations of bias in publications.
Therefore, those who mostly reference themselves, and a few carefully
selected cronies, and who habitually exclude a range of other workers
publishing in the same field, certainly open themselves up to some
accusation of bias – not by me, Dr Wentz, but by anyone. Such people are
certainly deviating from the unwritten academic norm and such behaviour is
anomalous precisely to the degree that it seems to treat the academic
community with contempt. I am sure that anyone viewing this matter in a
neutral and detached manner would have to agree with these perfectly valid
points, which are indeed the points that inspired my first email on this
matter. I do not know Dr Lewith, am not in any way associated with him,
and nor do I have much deep interest in his work. I merely pointed to what
seemed to be an unfortunate pattern. I have no money on any runner in this
race and idly watch it in a detached manner; if I can be proven wrong in
what I have said, then I will gladly apologise.
Instead of petulantly demanding apologies, perhaps Dr Wentz will now
supply all the requested data, and as an academic librarian, explain why
he approves and defends such anomalous referencing behaviour.
Sources
[1] BMJ letter, Reinhard Wentz, Using Citation figures Carefully, 15
July 2001
http://www.bmj.com/cgi/eletters/322/7302/1574#EL8
[2] BMJ letter, Peter Morrell, Slight trouble with figures..., 11
July 2001
http://www.bmj.com/cgi/eletters/322/7302/1574#EL7
[3] BMJ 1995; 311:688 (9 September), Letters, Ethical imperative to
publish extends to academics too, David Horrobin
http://www.bmj.com/cgi/content/full/311/7006/688/a
Competing interests: No competing interests
We commend Irnich et al for their effort, and for trying to account for the placebo effect.
Whatever the merits of their study, there is a more important question: Why examine traditional Chinese acupuncture when its application
varies so widely from one practitioner to another? Effective treatment of pain, like any symptomatic complaint, requires a medical diagnosis. Traditional acupuncture does not include a medical examination, and so cannot provide a correct diagnosis.
The study notes that acupuncture is more effective against the allodynia in myofascial pain
syndrome (1). This agrees with our observations at the Institute for the Study and Treatment of Pain, where virtually all patients consistently show physical signs of peripheral
neuropathy (2). These non-nociceptive signs do not appear on routine laboratory tests, but require a trained examiner. Needle therapy
seems to work through the peripheral nervous system because these clinical signs disappear following effective
treatment (3). We have found needling most effective when applied to tender, shortened muscles in affected
segments (4). We call our technique Intramuscular Stimulation (IMS) (5). Because IMS dry needling resolves clinical signs that are objective, how relevant are subjective reports, such as symptoms and placebos?
Meaningful research on chronic pain requires a distinction between ongoing nociception and increased sensitivity in allodynia. The problem in this debate stems from the absence of proper examination and diagnosis. Any treatment is "sham" without proper examination and diagnosis.
C. Chan Gunn, MD, PhD (hon.), DSc (hon.)
Clinical Professor, University of Washington
President, Institute for the Study and
Treatment of Pain
References
1. Gunn CC. Neuropathic Myofascial Pain Syndromes, Chapter 28 of Loeser JD et al, Bonica's Management of Pain, 3rd ed. Lippincott Willams & Wilkins, 2000
2. Gunn CC, Milbrandt WE. Early and Subtle Signs Low-Back Sprain. Spine Vol. 3 No. 3, 1978
The Matchstick Test -- The end of a matchstick produces firm indentations in
trophedema but not in normal skin. Trophedema often indicates neuropathy.
3. Gunn CC. Acupuncture and the peripheral nervous system -- Chapter 9 of Flishie J, White A. "Medical Acupuncture: A Western Scientific Approach" Churchill Livingstone, 1998
4. Gunn CC. Radiculopathic Pain: Diagnosis and Treatment of Segmental Irriation or Sensitization. Journal of Musculoskeletal Pain, Vol. 5(4) 1997
5. Gunn CC. The Gunn Approach to the Treatment of Chronic Pain 2nd ed. Churchill Livingstone, 1996
Competing interests: No competing interests
I am confused by the analysis in Irnich et al's randomised trial of
acupuncture.[1] They say that analyses were based on intention to treat
analysis. The figure showing progress through the trial shows that 56
patients were randomised to receive acupuncture, 60 massage, and 61 sham
laser. Yet for all the outcomes they analyse 51 patients, 57 and 57
respectively. Even if they include only those patients who completed the
trial (which surely is not the same as intention to treat?), the numbers
according to their figure should be 49 for acupuncture, 59 for massage,
and 57 for sham laser.
Is the figure wrong or did some patients get left out?
yours faithfully
David Lewis
1. Randomised trial of acupuncture compared with conventional massage
and "sham" laser acupuncture for treatment of chronic neck pain.
Dominik Irnich, Nicolas Behrens, Holger Molzen, Achim König, Jochen
Gleditsch, Martin Krauss, Malte Natalis, Edward Senn, Antje Beyer, Peter
Schöps, and Mike Cummings
BMJ 2001; 322: 1574
Competing interests: No competing interests
Sir,
Dr Lewith's team published a paper in 1981 on research methods in
acupuncture (Lewith GT, Machin D. A method of assessing the clinical
effects of acupuncture. Acupunct Electrother Res. 1981;6:265-76), which
suggests that his team's research interests in this subject go back to at
least 1980, well 'over 20 years' ago.
Dr Lewith is one of the authors of at least 70 papers published
between 1981-2001. He is the first author of some 50 papers, twelve of
which cite more than ten papers (range 11-115). In these papers he cites
himself on average 2.25 times (range 0-5) which suggests a mean self-
citation rate of 4.8%.
This is well within the range of what Peter Morrell considers ethical
in these matters.
I invite Peter Morrell to apologise to Dr Lewith.
Reinhard Wentz
Competing interests: No competing interests
Sir,
"We have been involved in the development of clinical trial
methodology within the field of acupuncture for over 20 years...Lewith, G
T., Machin D. On the evaluation of the clinical effects of acupuncture.
Pain 1983; 16: 111-27." [1]
Well, it is a great pity George Lewith cannot count so well [1] -
1983 to 2001 is NOT "over 20 years" but in fact, just 18. Furthermore, his
letter, not unusually [2], gives a rather high citation to his own
previous publications. In this case, it reaches the dizzy heights of 40%.
This self-citation rate, it must be said, is a tad on the high side; 1-5%
might seem more respectable.
I'm sure even Dr Lewith will agree that reading any book or article
with 40% references to the author's own publications, must make one
justifiably suspicious that such is a narrow field, constructed by only a
few and presided over by a small team of workers.
It is depressing to see that this practice has become quite
widespread within this so-called research field of complementary medicine,
where all the main figures seem to keep citing their own or each other's
work [3]. I fail to see how such a practice can attract any merit to this
topic or these researchers. It brings more like shame than merit. Nature
thrives on diversity.
Self-referencing invalidates the pluralistic basis of academic
discourse and in effect arrogantly declares that the opinions of a few are
superior to those of many; or, that one is blissfully ignorant of, or
despises, the work of others in the same field. Either way, such is surely
a contemptible attitude.
It should be universally condemned as a form of intellectual deceit,
and casts a shadow of doubt over every word they publish. I wish they
would seriously contemplate the bad impression imparted by such behaviour.
Sources
[1] BMJ letter, A critique of recent acupuncture trial methodology,
George Lewith, Peter White, Senior Research Fellow, Research
Physiotherapist University of Southampton (6 July 2001)
http://www.bmj.com/cgi/eletters/322/7302/1574#EL6
[2] Lewith in Australia
http://www.mja.com.au/public/issues/172_03_070200/lewith/lewith.html
4 out of 18 refs [22% self-citation]
Other Lewith BMJ articles:
http://www.bmj.com/cgi/content/full/322/7279/154
4 out of 23 refs [17.4% self-citation]
http://www.bmj.com/cgi/content/full/322/7279/131
1 out of 12 [8.3% self-citation]
http://www.bmj.com/cgi/content/full/309/6947/103
1 out of 11 [9.1% self-citation]
average here is 10 out of 64 = 15.6% [still way too high]
[3] Ernst article:
http://www.bmj.com/cgi/content/full/321/7269/1133
one of the very worst examples of high self-citation in this field;
16 to his own work out of 24 refs [66.7% self-citation] probably 10 times
'the norm', by no means untypical of his work and pretty outrageous.
Competing interests: No competing interests
Sir
We have been involved in the development of clinical trial
methodology within the field of acupuncture for over 20 years1. We feel
that Irnich et al's study as reported in the BMJ has methodological faults
which we hope to address in the context of our randomised controlled trial
that evaluates the effects of acupuncture versus a control treatment in
chronic mechanical neck pain and which will be completed later this year.
We note that there is a much fuller report of this trial on the BMJ
website.
This is effectively a large but negative study for acupuncture
according to the predefined primary outcome measure. However, the
treatment groups are inadequately balanced for primary diagnosis with
respect to myofascial pain; there were substantially fewer patients with
this diagnosis in the acupuncture group and acupuncture may be
particularly effective in this syndrome. We also have too little
information about the acupuncture and massage treatments to be able to
reproduce this study accurately. For instance we are unaware of which type
of traditional Chinese medicine was employed and we do not know if the
massage involved any stimulation over acupuncture points. The choice of
placebo/controls in acupuncture studies is a vexed and probably
unresolvable issue. Cummings suggests that sham laser is "a good
choice"2, but this is not substantiated by any evidence provided in other
studies although it appears to be credible in the context of this study.
Cummings' support for the "placebo needles" which we are currently
investigating in our research group in Southampton, is based on two small
studies from one research group3;4. We believe it is questionable,
particularly without detailed knowledge of the type of acupuncture
provided, whether the "placebo needles" described could be used
effectively and credibly in this study. Irnich et al have also suggested
that they measured ‘patients beliefs’ about treatment using a scale that
they attributed to Vincent5. We have used this credibility scale ourselves
in a number of studies6. The scale they used was originally designed and
validated by Borkovec and Nau7 and was intended to measure credibility of
treatment, not patients beliefs. The treatment provided by Irnich et al
was limited to 5 acupuncture sessions, possibly too little for effective
treatment8 . Outcome was not assessed continuously but every week, this
is unusual in a study involving acupuncture and chronic pain9;10. The
primary outcome measure does not appear to have been piloted or validated
prior to its use in the study. It involved change in pain related to
motion which was tested by one blinded assessor.
Unfortunately, no details
are given as to how this was effected. Were patients asked to repeat a
movement several times? Was a standardised set of instructions given? How
hard were they instructed to push? No information on intratester
reliability was offered and therefore the value of the primary outcome
must be questioned.
Unfortunately we believe this is a poorly constructed study with
unstratified treatment groups and poor primary outcome. It uses a
reasonable but under-evaluated placebo/control with limited and unclearly
described treatments. As a consequence it does not take us significantly
further forward in attempting to evaluate the specific effects of
acupuncture.
George Lewith MD FRCP
Senior Research Fellow, University of
Southampton
Peter White BSc MCSP
Research Physiotherapist
Reference List
1. Lewith GT,.Machin D. On the evaluation of the clinical effects of
acupuncture. Pain 1983;16:111-27.
2. Cummings M. Commentary: Controls for acupuncture - can we finally
see the light? British Medical Journal 2001;322:1578.
3. Streitberger K,.Kleinhenz J. Introducing a placebo needle into
acupuncture research. Lancet 1998; 352:364-5.
4. Kleinhenz J, Streitberger K, Windeler J, Gussbacher A, Mavridis
G, Martin E. Randomised clinical trial comparing the effects of
acupuncture and a newly designed placebo needle in rotator cuff
tendinitis. Pain 1999;83:235-41.
5. Vincent C. Credibility Assessment in Trials of Acupuncture.
Comp.Med.Res. 1990;4:8-11.
6. Vincent C,.Lewith G. Placebo controls for acupuncture studies.
Journal of the Royal Society of Medicine 1995;88:199-202.
7. Borkovec T,.Nau S. Credibility of Analogue Therapy Rationales.
J.Behav.Ther.and Exp.Psychiat 1972;3:257-60.
8. Ezzo J, Berman BM, Hadhazy V, Jadad A, Lao L, Singh BB. Is
acupuncture effective for the treatment of chronic pain? A systematic
review. Pain 2000;86:217-25.
9. Lewith G, Field J, Machin D. Acupuncture compared with placebo in
post-herpatic pain. Pain 1983;17:361-8.
10. Dowson D, Lewith G, Machin D. The effects of acupuncture versus
placebo in the treatment of headache. Pain 1985;21:35-42.
Competing interests: No competing interests
Results of reanalysis of Irinich trial using statistical methods of greater efficiency.
Editor
Irnich et al reported acupuncture superior to massage though not to
sham acupuncture for neck pain [1]. This suggests that acupuncture is
effective but that this is due to a placebo effect. The authors compared
improvements in pain between groups using pairwise t-tests. This
statistical method is of questionable efficiency. Firstly, It has been
amply demonstrated that regression analysis including baseline score as a
covariate has greater statistical power than comparison of change [2, 3].
Secondly, each pairwise comparison in a three group trial ignores one-
third of the patients; such comparisons are thus underpowered compared to
regression modelling of all data. Moreover, analysis of change scores,
such as that reported by Irnich, favors the group with worse baseline pain
scores (in this case, sham acupuncture) due to regression to the mean [4];
conversely, analysis of follow-up scores alone favors the group with lower
baseline pain. Regression analysis gives similar results regardless of the
direction of baseline imbalance.
Dr Irnich kindly provided me with raw data for reanalysis. To compare
the effects of treatment on pain score one week after treatment (the
prespecified primary outcome measure) I undertook a linear regression
analysis. The covariates used were baseline score, treatment group and the
following diagnostic variables: somatization, depression, history of
trauma, pain localization, pain site (neck / other), pain type (relived by
heat: yes or no), concomitant symptoms, neurological findings, diagnosis
(myofascial v other). Treatment was coded as two dummy variables: use of
any acupuncture technique and use of true acupuncture. Acupuncture, sham
laser and massage were thus coded 1, 1; 1, 0 and 0, 0 respectively. This
analysis estimates the effects of acupuncture needling and placebo effects
of acupuncture independently. Backwards stepwise regression was used where
a p value of 0.05 was the criterion for keeping a variable in the model.
Analyses were conduced on Stata 6 (College Station, Texas).
Depression, baseline score and use of true acupuncture remained in
the final regression model. The interpretation is that acupuncture
needling is of benefit in neck pain and that this is not attributable to a
placebo effect. Patients receiving true acupuncture had improvements in
pain, adjusted for baseline score and presence of depression, of 11.5
points (95%CI 3.5, 19.5; p=0.005) more than those in the massage and sham
groups. Restricting the analysis to patients who received either sham
laser or true acupuncture, acupuncture led to a reduction in pain score,
adjusted for baseline pain, of 9.4 points greater than sham (95%CI 0.9,
18.0; p=0.031). These results differ substantively from those reported in
the original paper.
Andrew Vickers
Memorial Sloan-Kettering Cancer Center
References
1 Irnich D, Behrens N, Molzen H, Konig A, Gleditsch J, Krauss M, Natalis
M, Senn E, Beyer A, Schops P. Randomised trial of acupuncture compared
with conventional massage and "sham" laser acupuncture for treatment of
chronic neck pain. BMJ 2001;322(7302):1574-8
2 Frison L, Pocock SJ. Repeated measures in clinical trials: analysis
using mean summary statistics and its implications for design. Stat Med
1992; 11:1685-1704
3 S Senn. Statistical Issues in Drug Development. Chichester: John Wiley
1997.
4 Bland JM, Altman DG. Regression towards the mean. BMJ
1994;308(6942):1499
Competing interests: No competing interests