Rapid Responses to:
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Rapid Responses: Rapid Responses published:
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Plantar Faciitis - No Further Research?
- James D. Michelson (11 July 2003)
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SWT for orthopaedic complaints: a total ban?
- Frank J.J. Conijn (13 July 2003)
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ESWT for Plantar Fasciitis - Conclusions Appropriate?
- Jan D. Rompe (18 July 2003)
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Correction on previous comment
- Frank J.J. Conijn (23 July 2003)
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Poor studies may yield poor results
- Brian Day (20 August 2003)
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James D. Michelson, Professor, Orthopaedic Surgery George Washington University School of Medicine
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To the Editor, I read the paper by Haake, et al., with great interest, hoping that some of the uncertainty surrounding the use of extracorporeal shock wave therapy for plantar fasciitis would be clarified. Although the authors state that there study is definitive, and that they therefore recommend against any further experimental testing of this treatment modality, there are sufficient methodological flaws in their study as to render their conclusions questionable. The study was well designed from the standpoint of randomization, blinding of the participants, and clinical inclusion criteria related to symptoms. What they fail to highlight, and is not apparent until one examines Table B (which was not published in print but is available online) is that less than half of their patients received what would generally be considered to be minimal conservative care that includes stretching exercises and casting/night splinting prior to their inclusion in the study. Such interventions have been shown to be effective 1;2, with failure of such treatment to be an essential aspect of the inclusion criteria for treatment by extracorporeal shock wave therapy. Including such patients in this study therefore violates one of the precepts of extracorporeal shock wave therapy, that is: failure of previous standard conservative care. It should be noted that getting physical therapy is not a substitute for stretching exercises as the former occurs a few time a week, while the latter is performed 3 to 4 times per day. The end-point assessment makes much of the various, unvalidated, rating scales for heel pain. What brings the validity of the rating scales into question is the observation that 56% of the placebo group required further treatment, compared to 56% of the treatment group (p<.008, Chi- square). Obviously, demonstrating equivalence of outcome at the final followup is uninterpretable due to the treatment bias during the followup period. In light of these issues, while I commend the authors on their efforts, I can not agree with them that this study is so definitive as to preclude further research in the field. Reference List 1. Pfeffer, G., Bacchetti, P., Deland, J., Lewis, A., Anderson, R., Davis, W., Alvarez, R., Brodsky, J., Cooper, P., Frey, C., Herrick, R., Myerson, M., Sammarco, J., Janecki, C., Ross, S., Bowman, M., and Smith, R.: Comparison of custom and prefabricated orthoses in the initial treatment of proximal plantar fasciitis. Foot Ankle Int. 20:214-221, 1999. 2. Wapner, K. L. and Sharkey, P. F.: The use of night splints for treatment of recalcitrant plantar fasciitis. Foot. Ankle. 12:135-137, 1991. Competing interests: None declared |
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Frank J.J. Conijn, Editor, Physical Therapist's Literature Update 1068 CE Amsterdam, The Netherlands
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To the Editor, I should like to comment on the conclusion by Dr. Haake and colleagues
(1). They treated 272 patients with plantar fasciitis with either shock
wave therapy (SWT) or placebo and found no significant efficacy difference.
It would therefore have been justified to conclude that shock wave therapy
(SWT) should not be used in orthopaedic conditions unless there is evidence
for its efficacy. However, they stated/concluded: "We cannot recommend
specific applications of extracorporeal shock wave therapy to be tested
in further clinical studies because all major trials, using
different shockwave variables and types of lithotripters, showed negative
results" (emphasis FC). The latter would not be true. According to Medline,
12 applicable randomized controlled trials (RCTs) have been done with SWT
in orthopaedic conditions (see the below table).
While the table would invoke a negative verdict in that the majority of the trials show negative results, it also shows that in calcific conditions SWT could well be effective. From a technical point of view, this should not be remarkable, since SWT is able to pulverize urogenital and gallbladder stones. Therefore, in contrast to Haake et al's opinion (1), research on SWT should in my view continue, with calcific conditions such as calcific shoulder tendinopathy and heel spur. Nevertheless, such research should also include seemingly more economic methods, such as needle aspiration and/or depositing a steroid in calcific shoulder conditions. And ultrasound, since Ebenbichler et al (14) found that to be effective in calcific shoulder tendinopathy, without any study being published -- to the knowledge of the current author -- that would suggest otherwise in calcific conditions. Although the 24 treatments Ebenbichler et al used would not be highly cost-effective, they used a dosage that can be increased to a great extent, when ultrasound is to be used in heel spur. For now, clinicians should in my view first determine whether a calcification
is present, before SWT treatments are referred for, advocated, applied
or reimbursed. It seems conclusively proved that SWT is not effective in
non-calcific orthopaedic conditions. For that, Dr. Haake deserves due credit
and honour, looking at the number of (high-quality) studies he did.
References: 1. Haake M, Buch M, Schoellner C, Goebel F, Vogel M, Moeller I, Hausdorf
J, Zanzow K, Schade-Brittinger C, Mueller HH. Extracorporeal shock wave
therapy for plantar fasciitis: randomised controlled multicentre trial.
BMJ 2003 July 12;327(7406):75-80. [Free
Full Text]
Frank J.J. Conijn, PT
Competing interests: None declared |
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Jan D. Rompe, Professor Dept. of Orthopaedic Surgery, Johannes gutenberg University of Medicine, D-55131 Mainz, Germany
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To the Editor: I read with great interest the article by Michael Haake and his co- workers. I would like to congratulate the authors on the study design and on the results of their outstanding multicentre trial. Nevertheless, I cannot agree with the drastic conclusions drawn (1) "ESWT is ineffective in the treatment of chronic plantar fasciitis", (2) "We cannot recommend specific applications of ESWT to be tested in further clinical studies". Though well designed from the standpoint of randomization, blinding of the participants, and inclusion criteria related to symptoms the results do not justify a ban on further research. The authors themselves made clear in the discussion that "the results are only valid for the therapeutic variables applied". Definitely, a generalization of their results is inappropriate: In the most recently published study (Reference #1) from our department forty-five running athletes with intractable plantar heel pain were enrolled in a randomized single-blind trial with a parallel-group design and blinded independent observer, to evaluate the efficacy of three applications of 2000 impulses of low-energy shock waves (Group I) compared with sham treatment (Group II). Followup examinations were done at six months, and at one year after extracorporeal shock wave application. Symptoms had been present from one year to six years. Each patient satisfied numerous inclusion and exclusion criteria before he or she was accepted into this study. The primary efficacy endpoint was reduction of subjects´s self-assessment of pain on first walking in the morning on a visual analog scale (range, 0 - 10 points) at six months after shock wave application. After six months self-assessment of pain on first walking in the morning as primary efficacy endpoint showed a significant reduction from an average 6.9 to 2.1 points in Group I, and from an average 7.0 to 4.7 points in Group II on the visual analog scale. The mean difference between both groups was 2.6 points. After twelve months pain on first walking in the morning showed a further reduction in both groups, to an average 1.5 points in Group I, and to 4.4 points in Group II . In conclusion, this study showed that three treatments with 2100 impulses of low-energy shock waves were a safe and effective nonsurgical method for treating chronic plantar fasciitis in long-distance runners after a followup of six months. The results were only valid for the therapeutic variables applied. This study sharply contrasted with the trial published by Buchbinder et al. in JAMA 2002 (Reference # 2). They enclosed 166 patients in a double-blind, randomized, placebo-controlled trial. Patients were randomly assigned to receive either ultrasound-guided ESWT given weekls for 3 weeks to a total dose of at least 1J/mm² or identical placebo to a total dose of 0.006 /mm². After significant improvements in both groups, the between- group difference of improvement was only 0.6 on a 100 mm visual analog scale. There was no evidence of ESWT over placebo. The study of Buchbinder was of excellent quality but there were clear differences regarding our trial. First, patients in the active group did not receive identical treatment (either 2000 or 2500 shock waves per treatment of energy levels varying between 0.02 mJ/mm² and 0.33 mJ/mm²) contrary to the current study (Refernce # 1). Second, the mean dose in the active group was 1407 mJ/mm², 500mJ/mm² more than in the current study. In the experience of the author of the current study patients will not tolerate such a high dose unless the treatment area of maximal pain is missed. Accordingly, third, Buchbinder did not focus on the area of maximal pain like in the current study, but on the area of maximal thickness of the plantar fascia. Fourth, a potent analgetic drug was allowed for the duration of the study. Fifth, patients were enrolled with a pain history as short as 6 weeks, contrary to 12 months in the current study. Sixth, there was no real placebo group, but sham therapy consisted of application of 100 shock waves of 0.02 mJ/mm². With regard to Haake´s publication the study design is excellent. However, his treatment regimen is clearly different from the regimen applied in our trial (reference # 1) regarding shock wave device, number of shock waves, energy flux density, technique of focussing, period between application, permission of additional pain medication, simultanoeus application of local anesthesia. The influence of simultaneous local anesthesia has been discussed particularly (Reference # 3). Auersperg et al. reported they had enrolled fifty-one patients with a chronic plantar fasciitis in a randomized controlled observer-blinded trial. Patients were randomly assigned to receive either active ESWT without local anesthesia, given daily for 3 days (Group I, n=25; 3 x 1500 pulses, total energy flux density 0.04 mJ/mm2) or identical ESWT with local anesthesia (Group II, n=26). Main outcome measures were: Pain during first step in the morning (measured on a 0-10 point visual analog scale), and no further therapy needed, measured at six weeks after the last ESWT. At six weeks, there was significant improvement in pain during first steps in the morning in both groups, by 4.4 points in Group I, and by 2.6 points in Group II. The mean between- group difference of improvement was 1.8 points. In Group I 19/25 (76%) patients didn´t need any further therapy compared with 9/26 (35%) patients in Group II. In conclusion, at six weeks success rates after low-energy ESWT with local anesthesia were significantly lower than after identical low-energy ESWT without local anesthesia. So, many questions still remain to be answered by future prospective randomized controlled trials: Has a local anesthetic an adverse effect on the clinical outcome after repetitive low-energy ESWT? What about performing the treatment under regional anesthesia? Is there an adverse effect of additional pain medication on the clinical outcome after repetitive low-energy ESWT? If so, why and to which extent? Is clinical outcome after repetitive low-energy ESWT comparable with results after high-energy ESWT performed under regional anesthesia? Once again, while I congratulate the authors on their efforts, the diverging results of the existing RCTs do not justify a ban on further research. On the contrary, they are a magnificent basis for future trials according GCP and ICH crriteria. References #1: Rompe JD, et al. Shock wave application for chronic plantar fasciitis in running athletes – a prospective, randomized, placebo- controlled trial. Am J Sports Med 31:268-275, 2003 #2: Buchbinder R, et al. Ultrasound-guided extracorporeal shock wave therapy for plantar fasciitis. JAMA 288: 1364-1372, 2002 #3: Auersperg V, et al. Influence of simultaneous local anesthesia on the outcome of repetitive low-energy shock wave therapy for chronic plantar fasciitis. Presentation at the 3rd Tri-National Meeting of the Austrian, Swiss, and German Societies for ESWT, Munich 2003 Competing interests: None declared |
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Frank J.J. Conijn, Editor, Physical Therapist's Literature Update 1068 CE Amsterdam, The Netherlands
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To the Editor, I have to correct my previous comment. The overview in it says that the study by Dr. Haake and colleagues (1) excluded patients with heel spur. I concluded that on the basis of the diagram "Flow of patients through trial" in the full text, which says that patients with dorsal heel spurs were excluded. After having found the Inclusion & Exclusion Criteria (which was on the web site, but not within, or even linked from within, the full text), I now see that the authors very probably meant an achilles spur with 'dorsal heel spur'. The criteria clearly state that all patients had to have had a radiologically proved (plantar) heel spur for inclusion. (Another item that should be corrected is that the abstract of the study by Dr. Speed and colleagues on Shock Wave Therapy [SWT] in shoulder tendinitis did state that the study concerned non-calcific shoulder tendinitis, even though this would only add to the evidence. Furthermore, the study by Prof. Rompe and colleagues (14) should be added. That study was not given by PubMed in the list of randomized trials on SWT [it had/has not been indexed yet].) The table should therefore look as follows:
The change regarding Dr. Haake et al's study means that the hypothesis that SWT is significantly effective in calcific orthopaedic conditions is much less likely true, despite the majority of trials on such calcific conditions still suggesting so. On the other hand, the hypothesis that SWT is ineffective in non-calcific conditions still stands, and ever stronger so after the change regarding study number 10. I would, nonetheless, still disagree with Dr. Haake et al's conclusion
that SWT should not be studied anymore. I would, and most certainly
so, agree that SWT should only be applied and reimbursed in (high-quality)
randomized trials, as Dr. Haake recently concluded (15). I could even go
as far as to say that only calcific conditions would be eligible for such
studies.
I would like to emphasize that I do not have any interests in SWT or
the manufacturers of the devices. I would, however, think that great
savings can be accomplished if therapies are developed that can prevent surgery (no disrespect intended whatsoever).
References: 1. Haake M, Buch M, Schoellner C, Goebel F, Vogel M, Moeller I, Hausdorf
J, Zanzow K, Schade-Brittinger C, Mueller HH. Extracorporeal shock wave
therapy for plantar fasciitis: randomised controlled multicentre trial.
BMJ 2003 July 12;327(7406):75-80. [Free
Full Text]
Frank J.J. Conijn, PT
Competing interests: None declared |
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Brian Day, Associate Professor University of British Columbia
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This paper contains significant errors in the study design which precluded any likelihood of the authors reaching scientifically valid conclusions. The study is a lesson in the axiom that while it is important to enlist the help of clinical trials experts and statisticians in designing a study protocol, it is equally important to ensure that participating clinicians are familiar with both the disorder being treated and (in the case of medical devices) with the technology being used. The methodology used in this study was seriously flawed. Ultrasound imaging and local anaesthesia should never be used, especially with a device (Dornier Epos) that has a very small “footprint”. The success of this method of treatment is dependant on delivering an adequate dose of energy to the site of pathology. That site is determined clinically by palpation as the point of maximal pain and tenderness. One cannot elicit tenderness if the site is anaesthetized and one cannot image pain with ultrasound. In the recommended protocols for low energy shock wave therapy, attention must be given to the technique of “clinical focusing” 1. Clinical focusing is effective only if refocusing is performed every 200–300 shocks with patient feedback to ensure that the energy is directed precisely to the area of treatment. A millimeter or 2 of movement away from the painful site will render a treatment ineffective. I conclude that the appropriate treatment site may not have been accurately targeted using the described protocol. History has a habit of rejecting new technologies and 15 years ago shockwave therapy for urolithiasis was met with initial skepticism. It is now recognized as one of the most effective and valuable non-invasive tools that urologists have. We have had experience now with over 6000 treatments using low dose shockwave therapy, and three manuscripts based on our clinical series have now been accepted for publication. I believe that larger, better designed, long term studies will prove the same is true for the orthopaedic applications of this technology. Carpenters should always first learn to use their tools, and physicians need to familiarize themselves with technology before they treat patients or conduct trials. To undertake a clinical trial (especially involving a placebo control group) whose methodology is so flawed that meaningful conclusions cannot be made is, in my view, unethical. The ethical issues relating to such trials have been discussed by Weijer 2. To suggest that we do not even study the technology further on the basis of this study is, in my opinion, ridiculous. Yours sincerely, Brian Day, MD, References: 1. Day B: Clinical Focusing and Low Energy ESWT in the Treatment of Work Induced Chronic Lateral Epicondylitis Proceedings of the 5th International Congress of the ISMST. www.ismst.com/events/2003_orlando_program.htm 5. Weijer C: Placebo trials and tribulations. CMAJ 2002: 603-604. Competing interests: None declared |
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