Effects of glucosamine, chondroitin, or placebo in patients with osteoarthritis of hip or knee: network meta-analysis
BMJ 2010; 341 doi: https://doi.org/10.1136/bmj.c4675 (Published 16 September 2010) Cite this as: BMJ 2010;341:c4675
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I read with interest the latest contribution from BMJ(Ref 1) to the
debate of glucosamine and chondroitin on hip or knee osteoarthritis
involving the Wandel et al study (Ref 2).
However I am not sure (from the content of Rapid Response Ref 1) if
the members of the Post Publication Review Meeting is fully aware of
general points of contention by authors of Rapid Response to the study,
which is:
1. the analysis of glucosamine sulphate and hydrochloride should be
separate; most authors did not argue that the latter works.
2. the response of osteoarthritis of the hip vs the knee to
glucosamine sulphate is different; the knee appears to more responsive to
the therapy (since most research referenced in the study and the Rapid
Responses involved knee osteoarthritis)
In spite of the recent authors' response (Ref 3), I am not convinced
that the combined analyses and (as a result) the overly generalised
conclusion can be taken seriously. Just like the dangers of subgroup
analysis has been exposed in recent months by BMJ, indiscriminate
congregation of studies to enhance meta-analysis pool is also misleading.
References
1. Groves T. Report from BMJ post publication review meeting
http://www.bmj.com/content/341/bmj.c4675.full%20./reply#bmj_el_247719
2. Wandel S, Juni P, Tendal B, Nuesch E, Villiger PM, Welton NJ, et
al. Effects of glucosamine, chondroitin, or placebo in patients with
osteoarthritis of hip or knee: network meta-analysis. BMJ. 2010;341:c4675
3. Trelle S, Wandel S, Juni P. Response to the critical appraisal by
Helg AG. http://www.bmj.com/content/341/bmj.c4675.full/reply#bmj_el_246850
Competing interests: No competing interests
Here are the conclusions of our review of our handling of this paper:
The article:
The criticisms raised in the rapid responses mainly address the selection and inclusion of studies and the assumptions made by the authors in their modelling analyses. We concluded that these criticisms continue the debate but do not negate the findings of the study.
This article and its accompanying web extras on bmj.com gave an accurate and suitably cautious account of this study's findings, strengths, and limitations. The authors were particularly thorough and transparent in reporting their methods and justifying their assumptions. We noted, too, that the authors had posted an "authors' reply" Rapid Response addressing the criticisms directly (and since the review meeting they have posted another). However, at the review meeting we decided that the following statements in the article:
* at the end of the discussion section: "Coverage of costs by health authorities or health insurers for these preparations and novel prescriptions to patients who have not received other treatments should be discouraged."
* in the abstract: "Health authorities and health insurers should not cover the costs of these preparations, and new prescriptions to patients who have not received treatment should be discouraged"
were not directly supported by their data.
The process:
The paper went through detailed peer review and was seen by expert reviewers active in this field. It was also seen by a statistics editor with specific expertise in this type of research methodology, and was accepted at the BMJ's research manuscript committee meeting (subject to revisions, which the authors then made).
At the revision stage the authors responded thoroughly to all comments made by peer reviewers and the BMJ's research editors and statistics editor. One request was for the authors to conduct a standard meta-analysis in addition to their network meta-analysis. This additional analysis was published as web extra 2 alongside the article on bmj.com.
Overall conclusion from post publication review:
The paper was a scholarly and well reported piece of work by highly regarded researchers. The authors' conclusions about funding or prescribing these preparations seemed only indirectly based on their findings and did not add usefully to the article.
The article passed through a rigorous and appropriate peer review process.
As is the case for any scholarly work, it may or may not turn out in good time, and after much debate, to be wrong. We hold the view that science advances by testing, debate, and argument and we consider it unremarkable for some readers to hold different opinions from authors regarding methodology.
Lessons learned and actions we're taking:
We aim to tighten up implementation of our advice on writing structured abstracts for research articles, which reads as follows:
"conclusions - primary conclusions and their implications, suggesting areas for further research if appropriate. Do not go beyond the data in the article. Conclusions are important because this is often the only part that readers look at."
Competing interests: I am senior research editor at the BMJ and chair the weekly research manuscript meeting. Professor Doug Altman, the BMJ's senior statistics editor, declared before the post publication review meeting that he is well acquainted with and has recently been involved in research with two of the article's authors. Hence he did not comment during the review meeting.
Andreas Helg (1, 2) provides a detailed discussion of our network
meta-analysis which we address point-by-point below.
Helg is concerned about the inclusion of one short-term trial with
only 4 weeks of follow-up (3). We agree that this trial was planned with
too short a follow-up period to assess any mid or long term effects.
However, as our analysis allows for multiple follow-up assessments the
respective data contributes only to the first assessment period (less or
equal than 3 months in Figure 2 (4)) and has therefore no impact on the
relevant mid/long term estimates of treatment efficacy.
Helg states that in 4 of the 10 included trials average pain at
baseline was too low to detect a relevant decrease. We agree that the
potential to benefit from an analgesic intervention will depend on the
intensity of the pain experienced. However, the average pain estimate of
2.6 cm as described by Helg for one trial is still compatible with more
than 70% of patients having the potential to experience a decrease in pain
of 1 cm or more on a 10 cm VAS. The minimum of 4 cm on a visual analogue
scale (VAS) suggested by Helg assuming that "pain asymptotically
approaches on average a value [of] around 3.4 cm after one year or later"
is arbitrary and not based on sufficient evidence to our knowledge. A meta
-regression could theoretically be used to shed further light on this
issue but is hampered by the ecological fallacy and regression to the mean
(5).
Helg claims that the inclusion of the GAIT trial is disputable and
argues that based on the results of the celecoxib group the trial appears
not to be "sufficiently sensitive to detect the minimal clinically
important difference" and implies that it should have been excluded. This
argument is data driven and therefore invalid.
Further, Helg questions the inclusion of the GAIT trial for the
analysis of joint space narrowing because fewer then 100 patients were
assessed for joint space narrowing. As described in the methods section of
the article we selected trials with at least 100 patients with knee or hip
osteoarthritis per arm (4), based on the rationale described in a meta-
epidemiological study of osteoarthritis trials (6). Since study selection
was based on the primary outcome of pain, we included GAIT also for the
analysis of secondary outcomes.
Helg argues that "the placebo effect becomes a major determinant of
the observed effect when the later one is expressed in form of an effect
size". We already addressed this concern in our initial standard meta-
analysis of chondroitin trials where we showed that in chondroitin trials
effect sizes do not depend on the change of pain scores in the control arm
(7).
Helg questions our calculation of effect sizes for the secondary
outcome joint space narrowing. As described, we used the median pooled
standard deviation of included trials to derive an effect size in order to
achieve comparability among trials. Obviously, this will result in a
overestimation of the pooled standard deviation for 50% of the trials, but
this will be cancelled out by an an underestimation in the other 50% of
the trials. More important, however, is the fact that the primary analysis
was done on the original scale. Effect sizes were just added for ease of
interpretation without lessening any radiological effect, despite Helg's
claim.
Naturally, we agree that changes in joint space narrowing during
follow-up vary between patients. In the light of this variation, the
observed, non-significant difference of 0.1 mm is indeed minute. Helg's
suggestions to change outcome definitions may be considered in further
trials. The cutoff of 0.25 mm suggested by Helg may be valid (or not), but
it is completely arbitrary and other authors suggested different cutoffs.
Helg criticises that we did not differentiate between glucosamine
hydrochloride and sulphate but rather combined both for the main analyses.
We addressed this in the paper by performing a stratified analysis
according to type of glucosamine which showed no difference between
treatment effects of glucosamine hydrochloride and sulphate. Moreover,
when looking at the subgroup of sulphate trials only (Figure 3 of the
article) it is clear that even if we would have restricted the network to
sulphate trials only glucosamine sulphate had no clinically relevant
effect. In addition, the effect of including glucosamine hydrochloride
trials is minimal given that only one trial (GAIT (8)) contributed to the
analysis, and only with 6 month data.
We agree with Helg that trial arms within the same trial are
correlated. This complicates the analysis because multiple comparisons
derived from the same trial cannot be treated as if they were independent.
As described in the methods section of the article the model used for the
analysis "accounts for multiple comparisons within a trial when there are
more than two treatment arms" (4). The model is available at:
http://www.ispm.ch/index.php?id=bmj.
Helg is correct to state that we included a linear term for time to
explore possible time trends. This analysis was exploratory and by no
means the primary analysis, on which we based all our conclusions. As
described in the methods section of the article we assumed no particular
time trend for the primary analysis. Helg argues that pain curves over
time are shaped similarly to bioavailablity curves, with an established
maximum somewhere. A look at Figure 2 of our article (4) indicates that
there appears no such maximum. A linear term actually seems to provide the
best fit: a horizontal line near zero.
Helg puts then forward what he calls "fundamental concerns" regarding
our analysis. He reiterates that the GAIT trial contributed multiple
(dependent) trial arms to the analysis. As stated above, our model
accounts for the dependency of trial arms in multi-arm trials. The model
can be appraised at: http://www.ispm.ch/index.php?id=bmj. He also suggests
that our analyses including covariates were overfitted. As described in
the methods section of the article (4) we only performed univariate
analysis i.e. we included only one covariate at a time and see no
violation of any "mathematical rule regarding the minimum information
required to obtain reasonable results", as suggested by Helg.
Helg finally suggests having an independent panel assessing our
analysis. We are open to this suggestion if this exercise is not driven by
any conflicts of interest. All data are available on the BMJ website and
the model is available at http://www.ispm.ch/index.php?id=bmj though).
None of the authors have any conflicts of interest.
References
1. Helg AG. Critical appraisal of the meta-analysis by Wandel et al.
- clinical aspects (part 1). Accessed at
http://www.bmj.com/content/341/bmj.c4675.full/reply#bmj_el_243280 on Nov 8
2010.
2. Helg AG. Critical appraisal of the meta-analysis by Wandel et al.
- methodological aspects (part 2). Accessed at
http://www.bmj.com/content/341/bmj.c4675.full/reply#bmj_el_243282 on Nov 8
2010.
3. Noack W, Fischer M, Forster KK, Rovati LC, Setnikar I. Glucosamine
sulfate in osteoarthritis of the knee. Osteoarthritis Cartilage. 1994;2:51
-9. [PMID: 11548224]
4. Wandel S, Juni P, Tendal B, Nuesch E, Villiger PM, Welton NJ, et
al. Effects of glucosamine, chondroitin, or placebo in patients with
osteoarthritis of hip or knee: network meta-analysis. BMJ. 2010;341:c4675.
[PMID: 20847017]
5. Thompson SG, Smith TC, Sharp SJ. Investigating underlying risk as
a source of heterogeneity in meta-analysis. Stat Med. 1997;16:2741-58.
[PMID: 9421873]
6. Nuesch E, Trelle S, Reichenbach S, Rutjes AW, Tschannen B, Altman
DG, et al. Small study effects in meta-analyses of osteoarthritis trials:
meta-epidemiological study. BMJ. 2010;341:c3515. [PMID: 20639294]
7. Reichenbach S, Sterchi R, Scherer M, Trelle S, Burgi E, Burgi U,
et al. Meta-analysis: chondroitin for osteoarthritis of the knee or hip.
Ann Intern Med. 2007;146:580-90. [PMID: 17438317]
8. Clegg DO, Reda DJ, Harris CL, Klein MA, O'Dell JR, Hooper MM, et
al. Glucosamine, chondroitin sulfate, and the two in combination for
painful knee osteoarthritis. N Engl J Med. 2006;354:795-808. [PMID:
16495392]
Competing interests: No competing interests
In my rapid response [1] it is not assumed, as it is stated in [2],
that "It is ethical to deter patients from a potentially effective joint-
protective supplement." It is discussed in my rapid response, whether
natural glycosaminoglycans in a diet, containing their enhanced amount
(animal joints, chicken wings etc.), could act, from a biochemical and
pharmacological viewpoint, more or less equivalently to their artificial
analogues or precursors administered as drugs. More details are in [3].
1. Jargin SV. Oral chondroitin sulphate and glucosamine vs. diet
modification. BMJ Rapid Response of 30 September 2010
http://www.bmj.com/content/341/bmj.c4675/reply
2. Goh S. Re: Oral chondroitin sulphate and glucosamine vs. diet
modification; you are what you eat? BMJ Rapid Response of 12 October 2010
http://www.bmj.com/content/341/bmj.c4675/reply
3. Jargin SV. On the role of chondroprotective agents in
osteoarthritis: on the way to the evidence-based medicine (in Russian with
English summary). Travmatologia i Ortopedia Rossii 2010;57(3):179-182.
http://www.rniito.org/journal/2010_3/179-182.pdf
Competing interests: No competing interests
Pelletier et al and others question the exclusion of small studies,
even though we have recently shown in a meta-epidemiological study that
small studies will often distort results of meta-analyses of
osteoarthritis trials - with biases introduced by small trials being
particularly prominent for glucosamine and chondroitin trials [1]. The
issues of different types of glucosamine and of differences in the quality
and bioequivalence of examined preparations were examined in Figure 3 of
our report, without evidence to suggest that either will explain our
results. Giacovelli and Rovati suggest several errors in our
classification of trials, which we were unable to confirm after careful re
-examination of our data. The apparent misclassification of the trial by
McAlindon [2] regarding the type of glucosamine used is related to
ambiguities in published information. In the primary report of the trial
it is stated that "the switch from the Physiologics to Rotta glucosamine
product occurred at enrolment of the 163rd participant" [2]. In a
description of the preparations, it is confirmed that the Physiologics
preparation contained glucosamine sulfate. Since no correction of the
original trial report is available to date we continue to adhere to our
classification.
Contrary to the suggestions by all three groups, we have explored
thoroughly the variation of effect of preparations over time. Figure 2 of
our report and published results of accompanying statistical tests suggest
that there is no variation across time-points over and above of what is
expected by chance alone (p=0.93 for interaction between treatment effect
and time). With a tau-squared estimate of 0.04, between trial
heterogeneity was indeed low. We are unable to reproduce the I-squared
estimate by Reginster et al, but emphasise that the large size of included
studies means that I-squared estimates may be unduly inflated even though
the actual variation between trials is small [3].
The cutoffs used to delineate the minimal clinically important difference
were not based on Cohen's seminal work from the 1970s [4] as suggested by
Pelletier et al, but on the median minimal clinically important difference
found in recent studies in patients with osteoarthritis as referenced in
the methods section of our report. Even though we agree that treatment
effects of paracetamol are concerningly small, effect sizes found in large
trials of NSAIDs and paracetamol using identical outcome definitions as
those referred to in our report are larger than suggested by Giacovelli
and Rovati: -0.38 for oral NSAIDs (95% CI -0.49 to -0.27) and -0.25 for
paracetamol (95% CI -0.39 to -0.11) [1].
Observed treatment effects for both, glucosamine and chondroitin as
compared with placebo are irrelevant to undetectable. With the observed
differences in pain intensity of 0.3 to 0.5 cm between food supplements
and placebo on a 10 cm visual analogue scale, the distribution of pain
scores in patients receiving supplements and placebo are nearly identical
[4, 5]. Therefore, we continue to conclude that it would be impossible,
based on the reported pain intensity at the end of a trial, to determine
whether a patient was allocated to a food supplement or to placebo.
1 Nuesch E, Trelle S, Reichenbach S, Rutjes AW, Tschannen B, Altman
DG, et al. Small study effects in meta-analyses of osteoarthritis trials:
meta-epidemiological study. BMJ 2010;341:c3515.
2 McAlindon T, Formica M, LaValley M, Lehmer M, Kabbara K.
Effectiveness of glucosamine for symptoms of knee osteoarthritis: results
from an internet-based randomized double-blind controlled trial. Am J Med
2004;117:643-9.
3 Rucker G, Schwarzer G, Carpenter JR, Schumacher M. Undue reliance
on I(2) in assessing heterogeneity may mislead. BMC Med Res Methodol
2008;8:79.
4 Cohen J. Statistical power analysis for the behavioral sciences. 2
ed. Hillsdale: Lawrence Erlbaum, 1988.
5 Juni P, Reichenbach S, Dieppe P. Osteoarthritis: rational approach
to treating the individual. Best Pract Res Clin Rheumatol 2006;20:721-40.
Competing interests: No competing interests
Submitted 15 October 2010.
Vlad et al. (1) concluded from their meta-analysis that glucosamine
hydrochloride is not effective, but found an effect size of 0.44 for
trials looking at glucosamine sulphate. Their results did not differ
substantially from those of Towheed et al. (2). Thus, according to these
two meta-analyses glucosamine hydrochloride and glucosamine sulphate are
not the same. Nevertheless, Wandel et al. (3) conceived a network of
trials (see Fig. 1 in (3)) that does not differentiate between glucosamine
hydrochloride and glucosamine sulphate. Some may consider this as a
(biased) anticipation of one out of two possible results.
When glucosamine hydrochloride and glucosamine sulphate are treated
as two different active ingredients a rather different network results
that consists of two branches: a glucosamine sulphate branch with no
direct comparisons between this compound and any other intervention, and a
chondroitin branch inside of which only the four arm (five arm with
celcoxib) trial by Clegg et al. (4) resp. Sawitzke et al. (5,6) (GAIT)
contributes to the emergence of a network. It is most likely correct to
assume that another network at the outset would have let to different
results. Therefore, some may hold that Wandel et al. have accomplished the
wrong analysis. Some may also wonder whether it makes sense to carry out a
network meta-analysis when the glucosamine sulphate branch of the network
can only be linked to the other interventions via placebo and when in the
chondroitin branch the only comparisons with glucosamine hydrochloride and
the combination of the two are mathematically related because they all
derive from the same trial with the same placebo group.
To explore possible time trends, Wandel et al. included a linear term
for time as a covariate in the analysis. Thus, they assumed that the
effects increase or decrease linearly with time. This assumption, however,
does not correspond to the observations made in osteoarthritis trials (6-
9). Curves depicting the decrease of pain versus time resemble more a
first order kinetics and with time approach asymptotically a value between
2.1 (6) and 4.8 cm (8) (3.4 cm in (9)) on a VAS from 0 to 10.0 cm, with
the curves of the placebo usually decreasing slower and/or being shifted
to the right along the time axis (6,8-10). The curves depicting the
differences between the interventions and placebo look similar to those in
bioavailability studies: They show a time point of maximal difference. The
inclusion of a linear term for time is to simplistic. - Would anyone
compare the decrease in pain in the trial of Mazieres et al. (11) looking
into the symptomatic effect of chondroitin sulphate with the one in the
trial of Reginster et al. (12) examining primarily the disease modifying
effect of glucosamine sulphate, and in order to do so either extrapolate
the data from the trial by Mazieres et al. linearly to 36 months or
interpolate the data of the trial by Reginster et al. at 3, 6, or 9
months? What does not make sense in a single (indirect) comparison also
does not make sense in a network meta-analysis. Some, therefore, may hold
that linking the data with a linear term for time may only dilute the
maximal effects of the interventions at 3, 6, and 9 months.
Fundamental concerns regarding the network meta-analysis by Wandel et
al.:
(a) Mixed treatment comparisons usually include multiple different
(independent) pair-wise comparisons carried out simultaneously. GAIT
provided a total of 6 direct pair-wise comparisons to the analysis by
Wandel et al. These comparisons, however, are not independent from one
another as, firstly, the results of the different trial arms are
mathematically linked - they all relate to the same placebo group - and,
secondly, because they are influenced in the same way by the effects that
are specific for this study. Wandel et al. wrote that their model
"accounts for multiple comparisons within a trial when there are more than
two treatment arms", and cite the network meta-analysis by Cooper et al.
(13) which also included multi-arm trials. That meta-analysis, however,
was based on a much more complex and highly cross-linked network
consisting of a total of 19 trials. Six of them were multi-arm trials.
Furthermore, they looked at dichotomous outcomes (stroke and major or
fatal bleeding episodes), the incidence of which remains constant over
time, and not at a continuous outcome like pain that does not behave in a
linear way and changes over time with respect to baseline. Some,
therefore, may hold that citing a publication of another very different
network meta-analysis does not proof that the model used by Wandel et al.
is appropriate.
(b) Wandel et al. included 7 trial characteristics as covariates in their
analysis (8 covariates with the linear term for time). They, however,
never had more than 10 effect sizes at their disposal in any of the nine
time windows. Of course at 6 months one can carry out up to 16 indirect
comparisons, but due to the network structure of the pair-wise comparisons
they are not independent from one another. Some, therefore, may reckon
that Wandel et al. exceeded the limits of fundamental mathematical rules
regarding the necessary minimum of information required to obtain
reasonable results?
In light of the numerous replies and the well substantiated
considerations exposed by their authors and in light of our concerns with
this network meta-analysis presented above, we would like to ask the
editorial board to appoint 3 independent experts, a mathematician, a
biostatistician, and an experienced clinician with good knowledge of
statistics, to review this work once more, taking into account all the
replies, and to express a second opinion. The mathematician and the
biostatistician should be selected among those that have developed the
methodology of mixed treatment comparisons. We would regard the experts as
independent when they have never been co-author (i) with any of the
authors of the network meta-analysis, or (ii) with any co-author of any
other earlier publication of the same authors.
Andreas G. Helg, PhD (Dr. sc. nat. ETH)
IBSA Institut Biochimique SA, CH-6915 Pambio-Noranco, Switzerland
1. Vlad SC, LaValley MP, McAlindon TE, Felson DT. Glucosamine for
pain in osteoarthritis: why do trial results differ? Arthritis Rheum
2007;56(7):2267-77.
2. Towheed TE, Maxwell L, Anastassiades TP, Shea B, Houpt J, Robinson
V, et al. Glucosamine therapy for treating osteoarthritis. Cochrane
Database Syst Rev 2001;(1):CD002946.
3. Wandel S, Juni P, Tendal B, Nuesch E, Villiger PM, Welton NJ, et
al. Effects of glucosamine, chondroitin, or placebo in patients with
osteoarthritis of hip or knee: network meta-analysis. BMJ 2010;341:c4675.
4. Clegg DO, Reda DJ, Harris CL, Klein MA, O'Dell JR, Hooper MM, et
al. Glucosamine, chondroitin sulfate, and the two in combination for
painful knee osteoarthritis. N Engl J Med 2006;354(8):796-808.
5. Sawitzke AD, Shi H, Finco MF, Dunlop DD, Bingham CO 3rd, Harris
CL, et al. The effect of glucosamine and/or chondroitin sulfate on the
progression of knee osteoarthritis: a report from the
glucosamine/chondroitin arthritis intervention trial. Arthritis Rheum
2008;58(10):3183-91.
6. Sawitzke AD, Shi H, Finco MF, Dunlop DD, Harris CL, Singer NG, et
al. Clinical efficacy and safety of glucosamine, chondroitin sulphate,
their combination, celecoxib or placebo taken to treat osteoarthritis of
the knee: 2-year results from GAIT. Ann Rheum Dis 2010;69(8):1459-64.
7. Bjordal JM, Klovning A, Ljunggren AE, Slordal L. Short-term
efficacy of pharmacotherapeutic interventions in osteoarthritic knee pain:
A meta-analysis of randomised placebo-controlled trials. Eur J Pain
2007;11(2):125-38.
8. Scott DL, Berry H, Capell H, Coppock J, Daymond T, Doyle DV, et
al. The long-term effects of non-steroidal anti-inflammatory drugs in
osteoarthritis of the knee: a randomized placebo-controlled trial.
Rheumatology (Oxford) 2000;39(10):1095-101.
9. Kahan A, Uebelhart D, De Vathaire F, Delmas PD, Reginster JY. Long
-term effects of chondroitins 4 and 6 sulfate on osteoarthritis: the study
on osteoarthritis progression prevention, a two-year, randomized, double-
blind, placebo-controlled trial. Arthritis Rheum 2009;60:524-33.
10. du Souich P, Verges J. Simple approach to predict the maximal
effect elicited by a drug when plasma concentrations are not available or
are dissociated from the effect, as illustrated with chondroitin sulfate
data. Clin Pharmacol Ther 2001;70(1):5-9.
11. Mazieres B, Hucher M, Zaim M, Garnero P. Effect of chondroitin
sulphate in symptomatic knee osteoarthritis: a multicentre, randomised,
double-blind, placebo-controlled study. Ann Rheum Dis 2007;66(5):639-45.
12. Reginster JY, Deroisy R, Rovati LC, Lee RL, Lejeune E, Bruyere O,
et al. Long-term effects of glucosamine sulphate on osteoarthritis
progression: a randomised, placebo-controlled clinical trial. Lancet
2001;357(9252):251-6.
13. Cooper NJ, Sutton AJ, Lu G, Khunti K. Mixed comparison of stroke
prevention treatments in individuals with nonrheumatic atrial
fibrillation. Arch Intern Med 2006;166:1269-75.
Competing interests: The author is employed by and writing on behalf of IBSA Institut Biochimique SA, a manufacturer and distributor of a prescription drug with chondroitin sulphate.
Submitted 15 October 2010.
Wandel et al. (1) were very concerned about the quality (e.g.
concealment of allocation) of the trials they included in their analysis,
but very little about the validity of the results obtained in these trials
and the clinical baseline characteristics of the patients: In one trial
pain was assessed after only 4 weeks (2), too early for a SYSADOA to
develop its maximal effect; in 4 trials (3-6) pain at baseline was less
than 4.0 cm, in one trial only 2.6 cm (3), not enough to detect a decrease
of 0.9 cm considering that pain asymptotically approaches on average a
value around 3.4 cm after one year or later (7-9).
Most disputable, however, is how they made use of GAIT (7,10,11).
This trial included a celecoxib arm in order to assess its sensitivity to
detect a symptomatic effect and to exclude false negative results. In GAIT
celecoxib was superior to placebo only in the primary outcome and the
OMERACT-OARSI response criterion after 6 months (10), but not anymore
after 2 years (7). Its effect size at 6 months was only 0.13 (10), well
below the 0.37 pre-specified by Wandel et al. as a minimal clinically
important difference and also below the effect size of 0.44 found for
coxibs (12). Although this trial proved not to be sufficiently sensitive
to detect the minimal clinically important difference pre-specified by
Wandel et al. they included it in their analysis. - With respect to the
analysis of the radiological data GAIT also does not meet the pre-
specified criterion of 100 patients per arm - only between 59 and 80
patients per arm were assessed on a modified intention to treat basis
(11), not enough to detect such an effect according to the power
calculations by Michel et al. (3) and Kahan et al. (8) and the results
found later in their trials. Some, therefore, may ask themselves whether
it was correct to include GAIT in the analysis. But without GAIT, no
network meta-analysis.
In the 10 trials selected by Wandel et al. the placebo effects
expressed as relative change from baseline varied between +17 % (increase
of pain, in (6) at 24 months) and -64 % (decrease of pain, in (7) at 24
months), pain levels at baseline expressed on a VAS (0-10.0 cm) varied
between 2.6 (3) and 6.2 cm (13), and the gender distributions differed by
as many as 34 percent points. Effects on pain and function observed in
osteoarthritis trials are known to be influenced by the level of pain at
baseline, the radiologic stage of disease, the gender distribution, and in
particular also by the placebo effect. The placebo effect becomes a major
determinant of the observed effect when the later one is expressed in form
of an effect size. According to Zhang et al. (14) the placebo effect is
strongly influenced by the disease activity at baseline. Cooper et al.
(15) write in a publication (also cited by Wandel et al.) that "the
assumptions of a mixed treatment comparison analysis are that (i) study-
specific treatment effects are drawn from a common population
(exchangeable) and that (ii) heterogeneity is constant between the
different comparisons." Considering the very different placebo effects and
pain levels at baseline some may doubt that these assumptions are
fulfilled. Unfortunately, Wandel et al. only tested for heterogeneity with
respect to methodological aspects of the trials, but not with respect to
the clinical baseline characteristics or the placebo effects.
Wandel et al. calculated the effect sizes regarding the radiological
effect of chondroitin in the trials by Kahan et al. (8) and Michel et al.
(3) using a median pooled SD of 1.2 mm although the standard deviations in
these two trials had been available and are 0.6 and 0.5 mm, respectively.
Using a standard pooled SD for the calculation of effect sizes for the
radiological effect is not appropriate because different measurement
techniques with different measurement errors were used in the 6 trials
examining this effect. In this way the authors lessened the radiological
effect of chondroitin by as much as a factor 2.0 or 2.4, respectively.
We have outlined earlier that the calculation of effect sizes is not
suitable for the estimation of the radiological effect (16). Instead a
failure criterion should be defined and the radiological effect should be
expressed in terms of relative risk reduction. For example, in the trial
by Kahan et al. (8) a narrowing of the joint space by 0.25 mm - based on
the minimal clinically important difference of 0.37 SD units pre-specified
by Wandel et al. - can be regarded as a minimal clinically important
disease progression (SD = 0.6 mm, 0.37 x 0.6 mm = 0.22 mm). In this trial
the percentage of patients with radiographic progression (decrease in
minimum joint space width of > 0.25 mm) was significantly reduced in
the chondroitin group with respect to the placebo group (28% versus 41%; p
<0.0005; relative risk reduction 33% [95% CI 16-46%]). The number of
patients needed to treat was 8 (95% CI 5-17). Wandel et al. had always
judged this trial as being of high methodological quality, and it is the
only high quality trial with chondroitin included in the meta-analysis
that allows for an estimation of the symptomatic effect. Effect sizes for
pain reduction in this trial at 3, 6, and 9 months were 0.19, 0.22, and
019, respectively, i.e. higher than the 0.14 of paracetamol, the current
pharmaceutical first line therapy, and close to the effect size of 0.29
found for NSAIDs (12). There is probably no other pharmaceutical treatment
that offers such an effect that persists over 6 months with virtually no
side effects, apart maybe from glucosamine sulphate or hyaluronic acid.
Furthermore, at 6 months 29% of the patients with chondroitin experienced
a clinically relevant decrease of pain of > 80% from baseline, whereas
only 18% of the patients under placebo had such a benefit (p <0.001).
Andreas G. Helg, PhD (Dr. sc. nat. ETH)
IBSA Institut Biochimique SA, CH-6915 Pambio-Noranco, Switzerland
1. Wandel S, Juni P, Tendal B, Nuesch E, Villiger PM, Welton NJ, et
al. Effects of glucosamine, chondroitin, or placebo in patients with
osteoarthritis of hip or knee: network meta-analysis. BMJ 2010;341:c4675.
2. Noack W, Fischer M, Forster KK, Rovati LC, Setnikar I. Glucosamine
sulfate in osteoarthritis of the knee. Osteoarthritis Cart 1994;2:51-9.
3. Michel BA, Stucki G, Frey D, De Vathaire F, Vignon E, Bruehlmann
P, et al. Chondroitins 4 and 6 sulfate in osteoarthritis of the knee: a
randomized, controlled trial. Arthritis Rheum 2005;52(3):779-86.
4. Reginster JY, Deroisy R, Rovati LC, Lee RL, Lejeune E, Bruyere O,
et al. Long-term effects of glucosamine sulphate on osteoarthritis
progression: a randomised, placebo-controlled clinical trial. Lancet
2001;357(9252):251-6.
5. Pavelka K, Gatterova J, Olejarova M, Machacek S, Giacovelli G,
Rovati LC. Glucosamine sulphate use and delay of progression of knee
osteoarthritis: a 3-year, randomized, placebo-controlled, double-blind
study. Arch Intern Med 2002;162:2113-23.
6. Rozendaal RM, Koes BW, van Osch GJVM, Uitterlinden EJ, Garling EH,
Willemsen SP, et al. Effect of glucosamine sulphate on hip osteoarthritis.
Ann Intern Med 2008;148:268-77.
7. Sawitzke AD, Shi H, Finco MF, Dunlop DD, Harris CL, Singer NG, et
al. Clinical efficacy and safety of glucosamine, chondroitin sulphate,
their combination, celecoxib or placebo taken to treat osteoarthritis of
the knee: 2-year results from GAIT. Ann Rheum Dis 2010;69(8):1459-64.
8. Kahan A, Uebelhart D, De Vathaire F, Delmas PD, Reginster JY. Long
-term effects of chondroitins 4 and 6 sulfate on osteoarthritis: the study
on osteoarthritis progression prevention, a two-year, randomized, double-
blind, placebo-controlled trial. Arthritis Rheum 2009;60:524-33.
9. Scott DL, Berry H, Capell H, Coppock J, Daymond T, Doyle DV, et
al. The long-term effects of non-steroidal anti-inflammatory drugs in
osteoarthritis of the knee: a randomized placebo-controlled trial.
Rheumatology (Oxford) 2000;39(10):1095-101.
10. Clegg DO, Reda DJ, Harris CL, Klein MA, O'Dell JR, Hooper MM, et
al. Glucosamine, chondroitin sulfate, and the two in combination for
painful knee osteoarthritis. N Engl J Med 2006;354(8):796-808.
11. Sawitzke AD, Shi H, Finco MF, Dunlop DD, Bingham CO 3rd, Harris
CL, et al. The effect of glucosamine and/or chondroitin sulfate on the
progression of knee osteoarthritis: a report from the
glucosamine/chondroitin arthritis intervention trial. Arthritis Rheum
2008;58(10):3183-91.
12. Zhang W, Nuki G, Moskowitz RW, Abramson S, Altman RD, Arden NK,
et al. OARSI recommendations for the management of hip and knee
osteoarthritis Part III: changes in evidence following systematic
cumulative update of research published through January 2009.
Osteoarthritis Cart 2010;18:476-99.
13. Mazieres B, Hucher M, Zaim M, Garnero P. Effect of chondroitin
sulphate in symptomatic knee osteoarthritis: a multicentre, randomised,
double-blind, placebo-controlled study. Ann Rheum Dis 2007;66(5):639-45.
14. Zhang W, Robertson J, Jones AC, Dieppe PA, Doherty M. The placebo
effect and its determinants in osteoarthritis: meta-analysis of randomised
controlled trials. Ann Rheum Dis 2008;67:1716-23.
15. Cooper NJ, Sutton AJ, Lu G, Khunti K. Mixed comparison of stroke
prevention treatments in individuals with nonrheumatic atrial
fibrillation. Arch Intern Med 2006;166:1269-75.
16. Helg AG, De Vathaire F. How solid are the results of the meta-
analysis by Reichenbach et al. and its conclusions? Ann Intern Med 2009.
www.annals.org/content/146/8/580.abstract/reply#annintmed_el_44993.
Competing interests: The author is employed by IBSA Institut Biochimique SA, a manufacturer and distributor of a prescription drug with chondroitin sulphate.
Wandel et al. (1) have produced yet one more meta-analysis of
glucosamine in osteoarthritis (OA) in the absence of new evidence, when
either international (2) and European (3) organisations, or the Cochrane
collaboration (4) and individual scientific groups (5,6) have already
produced comprehensive ones, showing that glucosamine sulphate is
effective on knee OA symptoms when administered as a well regulated,
quality-controlled, prescription product (7).
So, what is new in this novel effort? Independent, master
methodologists have already commented on a previous study by these authors
using the same technique (8) that "Unfortunately, their statistical
methods are so complex that many are mystified by whether the conclusions
make sense" (9). Indeed, the network meta-analysis approach used by Wandel
et al. gives exactly the same results as a conventional meta-analysis when
the seven glucosamine trials are pooled inappropriately, since they are
completely different in terms of design, indication, duration, glucosamine
salt, formulation and related quality control, dose regimen and
pharmacokinetics: the complex technique adopted is not able to add
anything from the scientific point of view, but succeeds in making cloudy
the results of a wrongly conducted meta-analysis. And in fact, as already
stigmatized by clinical OA experts (10), heterogeneity rises to
unacceptable levels when all these different trials are pooled: this would
recommend to subgroup those that are similar in design and performed with
the same prescription product (11-13), which easily documents its
clinically relevant efficacy (6,10). Trial selection strategies to
decrease heterogeneity have been previously advocated also by Wandel and
colleagues (14), but they are now neglected for glucosamine because not
functional to their aim. Thus, additional expert comment to this group's
approach is currently even more relevant: "Another concern is that any
such meta-analysis combines evidence from trials that are substantially
different in their design..... These issues all raise concerns as to the
extent to which the meta-analysis conclusions can be trusted and to whom
the findings apply" (9).
Wandel et al. inappropriately discuss heterogeneity in their Bayesian
approach declaring it absent while actually they used a prior distribution
with a strong emphasis on a high heterogeneity. In addition, they base
their calculations on back transformations to differences on a 10 cm
visual analogue scale (VAS). In this respect, the use of the minimal
clinically important difference expressed on a 10 cm VAS is certainly
attractive, but as long as one can rely on the original patient data.
Conversely, Wandel et al. derive it from a series of artificial back
transformations from the effect size (ES). As a consequence, while prior
informing the reader that the minimal clinically relevant ES is 0.20 in
any meta-analysis (15), surprisingly they then take the threshold up to
0.37 based on their artificial transformations: it is of note that in the
most recent evidence-based recommendations and meta-analysis from the
Osteoarthritis Research Society International (2), a mainstay of OA
pharmacological treatment such as paracetamol has an ES of 0.14, while
NSAIDs are at 0.29, i.e. the same as in glucosamine sulphate high quality
trials (2). In the latter studies, heterogeneity disappears when the three
long-term trials with prescription glucosamine sulphate (11-13) are
considered, with a clinically relevant ES of 0.27 on thorough pain
outcomes (6), or 0.34 (10) on the symptom parameters chosen by Wandel et
al. Indeed, these authors previously acknowledged that "the effect sizes
derived from meta-analyses of large randomized trials in OA are only small
to moderate for most therapeutic interventions, but this is still valuable
for patients and clinically relevant for physicians" (16), failing once
more to be now consistent with themselves.
Finally, the network meta-analysis technique has been developed
mainly to test the relative efficacy of drugs by indirect comparison, as
recently shown in rheumatology (17,18) and other fields (19): surprisingly
there is no such attempt by Wandel et al. Also, the claim of using
multiple observations over time within the same trial is misleading, since
the authors were able to use them only in 3 out of 7 studies; in addition,
their inclusion does not change the results, as we have tested in a series
of sensitivity analyses.
Giampaolo Giacovelli PhD, Head, Department of Biostatistics
Lucio C. Rovati MD, Chief Scientific Officer
Rottapharm | Madaus, Monza, Italy
References
1. Wandel S, Juni P, Tendal B, Nuesch E, Villiger PM, Welton NJ, et
al. Effects of glucosamine, chondroitin, or placebo in patients with
osteoarthritis of hip or knee: network meta-analysis. BMJ 2010;341:c4675.
2. Zhang W, Nuki G, Moskowitz RW, Abramson S, Altman RD, Arden NK, et
al. OARSI recommendations for the management of hip and knee
osteoarthritis: part III: Changes in evidence following systematic
cumulative update of research published through January 2009.
Osteoarthritis Cartilage 2010;18:476-99.
3. Jordan KM, Arden NK, Doherty M, et al. EULAR recommendations 2003:
an evidence based approach to the management of knee osteoarthritis:
report of a task force of the Standing Committee for International
Clinical Studies Including Therapeutic Trials (ESCISIT). Ann Rheum Dis
2003;62:1145-55.
4. Towheed TE, Maxwell L, Anastassiades TP, Shea B, Houpt J, Robinson
V, et al. Glucosamine therapy for treating osteoarthritis. Cochrane
Database Syst Rev 2009;2:CD002946.
5. Vlad SC, LaValley MP, McAlindon TE, Felson DT. Glucosamine for
pain in osteoarthritis: why do trial results differ? Arthritis Rheum
2007;56:2267-77.
6. Reginster JY. The efficacy of glucosamine sulfate in
osteoarthritis: financial and nonfinancial conflict of interest. Arthritis
Rheum 2007;56:2105-10.
7. De Wan M, Volpi G, inventors. A method of preparing mixed
glucosamine salts. US patent 5,847,107. 1997 Aug 13.
8. Stettler C, Wandel S, Allemann S, Kastrati A, Morice MC, Schomig
A, et al. Outcomes associated with drug-eluting and bare-metal stents: a
collaborative network meta-analysis. Lancet 2007;370:937-48.
9. Pocock SJ. Safety of drug-eluting stents: demystifying network
meta-analysis. Lancet 2007;370:2099-100.
10. Reginster JY, Altman RD, Hochberg MC. Prescription glucosamine
sulphate is effective in knee osteoarthritis. BMJ 2010; response to
341:c4675 (accessible online, at
http://www.bmj.com/content/341/bmj.c4675.full/reply#bmj_el_242366 ).
11. Reginster JY, Deroisy R, Rovati LC, Lee RL, Lejeune E, Bruyere O,
et al. Long-term effects of glucosamine sulphate on osteoarthritis
progression: a randomised, placebo-controlled clinical trial. Lancet
2001;357:251-6.
12. Pavelka K, Gatterova J, Olejarova M, Machacek S, Giacovelli G,
Rovati LC. Glucosamine sulfate use and delay of progression of knee
osteoarthritis: a 3-year, randomized, placebo-controlled, double-blind
study. Arch Intern Med 2002;162:2113-23.
13. Herrero-Beaumont G, Ivorra JA, Del Carmen Trabado M, Blanco FJ,
Benito P, Martin-Mola E, et al. Glucosamine sulfate in the treatment of
knee osteoarthritis symptoms: a randomized, double-blind, placebo-
controlled study using acetaminophen as a side comparator. Arthritis Rheum
2007;56:555-67.
14. Reichenbach S, Sterchi R, Scherer M, Trelle S, Burgi E, Burgi U,
et al. Meta-analysis: chondroitin for osteoarthritis of the knee or hip.
Ann Intern Med 2007;146:580-90.
15. Cohen J. Statistical power analysis for the behavioral sciences.
2nd ed. Lawrence Erlbaum, 1988.
16. Juni P, Reichenbach S, Dieppe P. Osteoarthritis: rational
approach to treating the individual. Best Pract Res Clin Rheumatol
2006;20:721-40.
17. Singh JA, Christensen R, Wells GA, Suarez-Almazor ME, Buchbinder
R, Lopez-Olivo MA, et al. A network meta-analysis of randomized controlled
trials of biologics for rheumatoid arthritis: a Cochrane overview. CMAJ
2009;181: 787-96.
18. Jansen JP, Bergman GJ, Huels J, Olson M. The Efficacy of
Bisphosphonates in the Prevention of Vertebral, Hip, and Nonvertebral-
Nonhip Fractures in Osteoporosis: A Network Meta-Analysis. Semin Arthritis
Rheum 2010 [Epub ahead of print].
19. Riemsma R, Forbes CA, Kessels A, Lykopoulos K, Amonkar MM, Rea
DW, Kleijnen J. Systematic review of aromatase inhibitors in the first-
line treatment for hormone sensitive advanced or metastatic breast cancer.
Breast Cancer Res Treat 2010; 123:9-24.
Competing interests: The authors are scientists from Rottapharm, maker of the proprietary formulation of prescription glucosamine sulphate. When contacted by Wandel et al. to provide data on their trials that are included in the meta-analysis, they immediately agreed to do so, but they were never contacted again afterwards.
The article by Wandel et al. (1) is a network meta-analysis of the
symptomatic and disease modifying effects of chondroitin sulfate,
glucosamine, and the combination of both compounds. The results of the
meta-analysis depend almost entirely on the inclusion and exclusion
criteria of the trials analysed. In addition, the interpretation of the
results depends upon the limits or thresholds defined as clinically
relevant.
In the study of Wandel et al. (1) the criteria used for the selection
of trials is questionable. For evaluation of slow acting drugs for
osteoarthritis, the European Medicines Agency guidelines recommend
evaluation of analgesia for at least 6 and 12 months, and after two years
for evaluation of the DMOAD effect (2). Wandel et al. (1) have not taken
into account the characteristics of the response of these drugs. Thus,
they have included the trial of Noack et al. (3) with a duration of 1 to 4
weeks, when it is well known that full effect of glucosamine and
chondroitin sulfate may not be apparent before 20 to 26 weeks.
Second, as in the previous meta-analysis by Reichenbach et al. (4),
the exclusion of small studies is highly questionable. In the present meta
-analysis, the authors have just considered trials with a minimum of 100
patients per arm. A more correct approach would have been performing a
different scenario analysis (sensibility) in order to assess the effects
with and without all the clinical data available.
Third, the authors do not take into account the baseline values of
pain and obviate this problem by mentioning the difference between
treatments. However, a difference in pain of 0.9 cm when the pain is
severe (>7 on a 0-10 cm VAS) is clinically different from the same
difference, when observed for intensities of pain <4; in the
chondroitin sulphate studies analysed, the mean baseline pain score was
2.5 (5), 4.0 (6) and 5.7 (7) on a scale of 0-10. Indeed, in the study of
Michel et al.5, designed to study the structure modifying effect of
chondroitin sulfate, it is unreasonable to expect that pain can decrease
>0.9 mm.
Fourth, the limits established to evaluate the results are poorly
justified; they are based on the cut-off values established in the 70's by
Cohen (8) for psychometric assessment, e.g. small effect = 0.20, moderate
effect = 0.5 and large effect = 0.80. Wandel et al. (1) have arbitrarily
defined as clinically relevant an effect size > 0.39 corresponding to a
change in pain of 1 cm. However, there is no evidence supporting that the
cut-off values established for psychometric measurements can be used to
assess clinical improvement in osteoarthritis, where effect sizes smaller
than 0.4 are routinely considered to be clinically meaningful. Indeed,
paracetamol is recommended for the initial treatment of symptomatic
osteoarthritis by the European League of Associations of Rheumatology and
the Osteoarthritis Research Society International, yet its effect size for
pain is <0.20.
Fifth, the statistical approach used by Wandel et al. (1) may be
jeopardised by the fact that the analgesic effect of chondroitin sulfate
and glucosamine is not uniformly distributed over time; eg, initially
there is no analgesia, followed by an analgesic effect and late fading of
analgesia (7). Figure 2 perfectly illustrates this point. Pain intensity
has been pooled at all time points assuming that the variation across time
points was not over and above what would be expected by chance and this,
as discussed previously, may not be correct. Moreover, it is crucial to
take into account what has a clinical significance and under this point of
view, pooling the response as a function of time does not appear adequate.
To assess the analgesic response of chondroitin sulfate and glucosamine,
the authors should have determined the effect at each time point,
preferably after 6 or 12 months, when the products may have reached their
full effect, so to capture the response more adequately.
The results and conclusions reported by Wandel et al. (1) about the
apparent lack of efficacy of glucosamine and chondroitin sulfate as
structure modifying drugs warrant further comments. According to the
criteria of Wandel et al. (1), the effect size reported for chondroitin
sulfate and glucosamine sulfate as DMOADs are not clinically meaningful.
Another meta-analysis9 evaluating the DMOAD effect of chondroitin sulfate
including the same three trials (5,7,10) considered in the meta-analysis
of Wandel et al. (1), reached the conclusion that the difference between
placebo and chondroitin sulfate in joint space width over 2 years was 0.13
mm (95% CI 0.06, 0.19) (P=0.0002), corresponding to an effect size of 0.23
(95% CI 0.11, 0.35) (P=0.0001); this effect size differs significantly
from that shown in the article of Wandel et al. (1). Taking into account
that baseline values of joint space width were 2.41 mm (2), 3.81 mm (4)
and 3.86 mm (11), a difference with placebo of 0.13 mm represents 3.4-5.4%
of baseline over two or three years, a value that may be clinically
meaningful for osteoarticular diseases. Indeed, in a study that included
follow-up for 5 and more years of the patients included in the randomized
placebo-controlled trials of glucosamine sulphate (11), the incidence of
knee replacement in patients who received glucosamine was 6.3%, less than
half the incidence observed in the patients on placebo, e.g. 14.5% (12),
clearly demonstrating that an effect size lower than 0.40 is clinically
meaningful when considering the DMOAD effect of chondroitin sulfate and
glucosamine sulfate.
Furthermore, regarding the combination of chondroitin sulfate and
glucosamine hydrochloride as was used in the Glucosamine Arthritis
Intervetion Trial, to perform a meta-analysis with only a single trial
(13) is questionable. Indeed, one of the objectives of a network meta-
analysis is to perform indirect comparisons between treatments that have
not been compared in a "head-to-head" fashion; herein, one could compare
directly the results of the glucosamine hydrochloride and the chondroitin
sulfate arms of the GAIT.
Finally, Wandel et al. (1) should have noted the limitations to the
methodology and approach used and how these limitations affect the ability
to make conclusions based on their results. We do not believe that they
can reach the conclusion that the use of pharmaceutically produced,
prescription branded chondroitin sulfate, glucosamine sulfate and their
combination should be discouraged for the management of patients with
symptomatic osteoarthritis of the knee.
Jean-Pierre Pelletier, MD, Professor of Medicine, Head, Division of
Rheumatology, University of Montreal, Canada
Marc C. Hochberg, MD, MPH, Professor of Medicine, Head, Division of
Rheumatology & Clinical Immunology, University of Maryland School of
Medicine, USA
Patrick du Souich, MD, PhD, Professor and Director, Department of
Pharmacology, Faculty of Medicine, University of Montreal, Canada
Andre Kahan, MD, PhD, Professor of Rheumatology, Paris Descartes
University, Faculty of Medicine, Head Department of Rheumatology A, Cochin
Hospital, AP-HP, France
Beat A. Michel, MD, Professor and Chair, Department of Rheumatology
and, Institute for Physical Medicine, University Hospital Zurich,
Switzerland
References
1. Wandel S, Juni P, Tendal B, Noesch E, Villiger PM, Welton NJ,
Reichenbach S, Trelle S. Effects of glucosamine, chondroitin, or placebo
in patients with osteoarthritis of hip or knee: network meta-analysis.
BMJ. 2010 Sep 16;341:c4675. doi: 10.1136/bmj.c4675.
2. Guideline on clinical investigation of medicinal products used in
the treatment of osteoarthritis. CPMP/EWP/784/97 Rev. 1; London, 23 April
2009.
3. Noack W, Fischer M, Forster KK, Rovati LC, Setnikar I. Glucosamine
sulfate in osteoarthritis of the knee. Osteoarthritis Cartilage. 1994
Mar;2(1):51-9.
4. Reichenbach S, Sterchi R, Scherer M, Trelle S, Burgi E, Burgi U,
Dieppe PA, Juni P. Meta-analysis: chondroitin for osteoarthritis of the
knee or hip. Ann Intern Med. 2007 Apr 17;146(8):580-90.
5. Michel BA, Stucki G, Frey D, De Vathaire F, Vignon E, Bruehlmann
P, Uebelhart D. Chondroitins 4 and 6 sulfate in osteoarthritis of the
knee: a randomized, controlled trial. Arthritis Rheum. 2005 Mar;52(3):779-
86.
6. Mazieres B, Hucher M, Za?m M, Garnero P. Effect of chondroitin
sulphate in symptomatic knee osteoarthritis: a multicentre, randomised,
double-blind, placebo-controlled study. Ann Rheum Dis. 2007 May;66(5):639-
45.
7. Kahan A, Uebelhart D, De Vathaire F, Delmas PD, Reginster JY. Long
-term effects of chondroitins 4 and 6 sulfate on knee osteoarthritis: the
study on osteoarthritis progression prevention, a two-year, randomized,
double-blind, placebo-controlled trial. Arthritis Rheum. 2009
Feb;60(2):524-33.
8. Cohen J. Statistical Power Analysis for the Behavioral Sciences.
2nd ed. Hillsdale, NJ: Lawrence Erlbaum Associates; 1988.
9. Hochberg MC. Structure-modifying effects of chondroitin sulfate in
knee osteoarthritis: an updated meta-analysis of randomized placebo-
controlled trials of 2-year duration. Osteoarthritis Cartilage. 2010
Jun;18 Suppl 1:S28-31.
10. Sawitzke AD, Shi H, Finco MF, Dunlop DD, Bingham CO 3rd, Harris
CL, Singer NG, Bradley JD, Silver D, Jackson CG, Lane NE, Oddis CV, Wolfe
F, Lisse J, Furst DE, Reda DJ, Moskowitz RW, Williams HJ, Clegg DO. The
effect of glucosamine and/or chondroitin sulfate on the progression of
knee osteoarthritis: a report from the glucosamine/chondroitin arthritis
intervention trial. Arthritis Rheum. 2008 Oct;58(10):3183-91.
11. Reginster JY, Deroisy R, Rovati LC, Lee RL, Lejeune E, Bruyere O,
Giacovelli G, Henrotin Y, Dacre JE, Gossett C. Long-term effects of
glucosamine sulphate on osteoarthritis progression: a randomised, placebo-
controlled clinical trial. Lancet. 2001 Jan 27;357(9252):251-6.
12. Bruyere O, Pavelka K, Rovati LC, Gatterova J, Giacovelli G,
Olejarova M, Deroisy R, Reginster JY. Total joint replacement after
glucosamine sulphate treatment in knee osteoarthritis: results of a mean 8
-year observation of patients from two previous 3-year, randomised,
placebo-controlled trials. Osteoarthritis Cartilage. 2008 Feb;16(2):254-
60.
13. Clegg DO, Reda DJ, Harris CL, Klein MA, O'Dell JR, Hooper MM,
Bradley JD, Bingham CO 3rd, Weisman MH, Jackson CG, Lane NE, Cush JJ,
Moreland LW, Schumacher HR Jr, Oddis CV, Wolfe F, Molitor JA, Yocum DE,
Schnitzer TJ, Furst DE, Sawitzke AD, Shi H, Brandt KD, Moskowitz RW,
Williams HJ. Glucosamine, chondroitin sulfate, and the two in combination
for painful knee osteoarthritis. N Engl J Med. 2006 Feb 23;354(8):795-808.
Competing interests: The authors received research funds and lecture fees from various pharmaceutical companies involved in the treatment of osteoarthritis with chondroitin and/or glucosamine.
Re: Effects of glucosamine, chondroitin, or placebo in patients with osteoarthritis of hip or knee: network meta-analysis
To all awaiting pharma-independent studies involving the effect of Glucosamine Sulphate on osteoarthritis of the knee:
The results of the LEGS study by Fransen is now available at
http://ard.bmj.com/content/early/2014/01/06/annrheumdis-2013-203954.shor...
Glucosamine and chondroitin for knee osteoarthritis: a double-blind randomised placebo-controlled clinical trial evaluating single and combination regimens
Abstract
Objective To determine if the dietary supplements, glucosamine and/or chondroitin, result in reduced joint space narrowing (JSN) and pain among people with symptomatic knee osteoarthritis.
Methods A double-blind randomised placebo-controlled clinical trial with 2-year follow-up. 605 participants, aged 45–75 years, reporting chronic knee pain and with evidence of medial tibio-femoral compartment narrowing (but retaining >2 mm medial joint space width) were randomised to once daily: glucosamine sulfate 1500 mg (n=152), chondroitin sulfate 800 mg (n=151), both dietary supplements (n=151) or matching placebo capsules (n=151). JSN (mm) over 2 years was measured from digitised knee radiographs. Maximum knee pain (0–10) was self-reported in a participant diary for 7 days every 2 months over 1 year.
Results After adjusting for factors associated with structural disease progression (gender, body mass index (BMI), baseline structural disease severity and Heberden's nodes), allocation to the dietary supplement combination (glucosamine–chondroitin) resulted in a statistically significant (p=0.046) reduction of 2-year JSN compared to placebo: mean difference 0.10 mm (95% CI 0.002 mm to 0.20 mm); no significant structural effect for the single treatment allocations was detected. All four allocation groups demonstrated reduced knee pain over the first year, but no significant between-group differences (p=0.93) were detected. 34 (6%) participants reported possibly-related adverse medical events over the 2-year follow-up period.
Conclusions Allocation to the glucosamine–chondroitin combination resulted in a statistically significant reduction in JSN at 2 years. While all allocation groups demonstrated reduced knee pain over the study period, none of the treatment allocation groups demonstrated significant symptomatic benefit above placebo.
Ann Rheum Dis doi:10.1136/annrheumdis-2013-203954
For your consideration
Competing interests: No competing interests