24-Febr Dear members of the BMJ Editorial team,

Transcription

1 24-Febr-2018 Manuscript ID BMJ entitled "A randomised sham controlled clinical trial of vertebroplasty for painful acute osteoporotic vertebral compression fractures (VERTOS IV)" Dear members of the BMJ Editorial team, We want to thank you for reviewing our manuscript. The comments and advises are constructive and helpful in improving the quality of the paper. We thank the reviewers their interest and their professional comments. In the following, we will answer point by point to all comments from the Editorial committee and the reviewers and indicating when changes are made in the paper. 1. We thought the trial was interesting and well done and reported. We note that no protocol was submitted with the paper, so please do upload a protocol when you return your revision. - The protocol will be uploaded with our revised paper. 2. The two groups seem somewhat unbalanced in terms of strong opioid consumption, while their mean VAS scores are similar. You might comment on this. - We thank the editors for pointing this out. In Ancillary analyses we replaced the log rank test with A Cox regression analysis showed no statistically significant differences in pain relief between the two groups at the 12-month follow-up after adjusting for the clinically important covariate strong opiate intake (HR= 1.022; 95% CI=0.9 to 1.2, Wald(1)= 0.06, p =0.80). p.16, l.14. We replaced Kaplan-Meier survival analysis with Cox regression analysis in the Statistical analysis chapter, p. 10, l An editor who practices as a primary care doctor commented that this evaluates a good clinical question. He noted that "From a primary care perspective, this is a common scenario and we may feel tempted to refer patients hastily for a neurosurgery consultation. So perhaps this helps us to counsel patients better and temper their (and our own) expectations." - Indeed, it was our purpose to look for an answer that helps the clinician in daily practice while evaluating the best treatment option for a patient. 4. We note that you didn't mention a previous Cochrane review on this topic. Perhaps it should be mentioned since the results are in line with your findings. Cochrane Database Syst Rev Apr 30;(4):CD doi: / CD pub2. Percutaneous vertebroplasty for osteoporotic vertebral compression fracture. "Based upon moderate quality evidence, our review does not support a role for vertebroplasty for treating osteoporotic vertebral fractures in routine practice. We found no demonstrable clinically important benefits compared with a sham procedure and subgroup analyses indicated that results did not differ according to duration of pain 6 weeks versus > 6 weeks. " - We thank the editors for this valuable comment. Although we were aware about this Cochrane review, one moment in time we erased it due to word count. We added it in the paper at p.18, l.16 in Discussion as This trial reinforces the results of two previous blinded trials5,6 and the Cochrane review about percutaneous vertebroplasty What was the timing of the PRIMARY outcome? Many are reported in the paper. The trial registration lists all of them (but then says time frame was 12 months. We think this is okay, but please clarify. One very important point is that we want all outcomes listed in the trial registration to be reported in the paper. Please identify any post-hoc outcomes as post-hoc. This is crucial since many trials that we publish are subject to the scrutiny of the COMPare project. It is better to avoid problems by making absolutely certain to report all prespecified outcomes and clearly flag post-hoc outcomes.

2 - We thank the editors for the comment. In order to be more clear about the primary/secondary objectives and post-hoc measurements we added as follows: - for the PRIMARY outcome we added prespecified in Outcomes at p.8, l.42; and we added the measurement time points respectively 1 day, 1 week, and at 1, 3, 6, 12 months after the procedure at p.8, l.44 - for the SECONDARY outcome we added prespecified in Outcomes at p.8, l.48 and the measurement time points respectively 1 week, and at 1, 3, 6, 12 months after the procedure at p.8, l the post-hoc outcomes are defined at p.9. l.27. We changed line p.9.l into: Post-hoc analysis included the proportion of patients in both groups at 12 months follow-up with the following post-hoc outcomes: VAS score of 5 or higher, progressive height loss of treated fractures (defined as 4 mm or more) and a new fracture. 5. You specify a difference of 1.5 points on the VAS as clinically meaningful difference (at 12 months). Both groups had a much larger difference! - First of all, in order to stay in line with the already published data we decided to use the same pre-assumptions in Methods regarding VAS as in the Invest (Kallmes et al.) and Vertos II (Klazen et al.) trials. Furthermore, in answer to your question we refer to the VERTOS 4 study registered at ClinicalTrials.gov., NCT , with the explanation in Methods: Methods Study design VERTOS IV is a multicenter RCT concerning the treatment of patients with a painful osteoporotic VCF. Patients are recruited on the Radiology departments of the participating hospitals and randomized to PV or a simulated procedure. Upon obtaining informed consent an independent central telephone operator completes the randomisation procedure, using a computer program. The maximum allowed unbalance (block size) is six, with a maximum sample size of 84 for each participating centre. A total of 180 patients will be enrolled, 90 in each group. This is based on the assumption of a 1.5 point difference in pain relief (VAS Score) and a 20% withdrawal rate (α = 0.05 and β = 0.20, 7 measurement points). The enrolment of patients will take place in four centres in The Netherlands: St. Elisabeth Ziekenhuis in Tilburg, Catharina Ziekenhuis in Eindhoven, Medisch Spectrum Twente in Enschede and Albert Schweitzer Ziekenhuis in Dordrecht. Randomization will start January 2011 with an expected completion of enrolment by January There is a one-year follow-up, with the possibility of an extended follow-up at two years. 6. We require a Data Sharing Statement for all clinical trials published in The BMJ. You must commit to sharing the relevant data upon reasonable request. If the paper is accepted after the revision our technical editors will let you know the exact wording. - We will wait for the exact wording and will add the Statement. 7. VAPOUR started also in 2011, was published in Was there an overlap? How much does THIS trial advance our understanding of the issues? Please comment. - Both trials started and ended approximately at the same time. - Both trials focus on osteoporotic acute vertebral compression fractures. However an important difference between the two trials is the fact that VERTOS 4 included outpatient ambulant patients with a VAS>5referred by the general practitioner, whereas VAPOUR included merely hospitalized inpatients with a VAS>7. This VERTOS 4 trial therefore is more in line with daily practice of general practitioners / BMJ readers. Please, see the improvements in the text, Section Strenths and Limitations (second paragraph) of the Discussion. 8. It should be principal and not principle findings in the discussion - We thank the editors for pointing out this mistake. We corrected principle at p.17 Reviewer: 1

3 Thank you for inviting me to review this interesting paper. This randomized double-blind clinical trial aims to explore the treatment efficacy of percutaneous vertebroplasty (PVP) for painful acute osteoporotic vertebral compression fractures, compared to sham procedure. Considering the high originality as well as importance of clinical work, I think it can be published on the BMJ after minor revision. Here are my detailed comments. * Originality: I think this research add enough to what is already in the published literature. According to the previous literatures, four important studies explored the treatment efficacy of PVP for osteoporotic vertebral compression fractures (OVCFs), which are the Australian, INVEST, VERTOS II, and VAPOUR trials, respectively. Each of the trials had its limitations, either with short-term follow up or mixed inclusion criteria that not reflect the real-word clinical practice. This trial, the VERTOS IV trial, overcame the limitations existed in the previous trials, with stricter inclusion/exclusion criteria, larger patient cohorts, longer clinical and imaging follow-up and no cross-overs. These improvements on the study protocol strength the trial s confidence level. * Importance of work to general readers: I think the work matters to clinicians, patients, teachers, and policymakers. Also, a general journal like BMJ is the right place for it. OVCFs occur frequently especially in the elderly worldwide. Although with debate, PVP is now considered as an important method on OVCFs. So, this research is with high importance of clinical work. * Scientific reliability Q: Research Question - clearly defined and appropriately answered? A: Yes. Overall design of study - adequate? 9. A: Yes. But I have an question that need the authors to answer. The authors used the model to analyze whether there was a significant interaction between treatment and time during 12 months follow-up period, and received the negative results. In my opinion, I am interested to know whether there was a statistical difference about VAS reduction at each follow-up time point between the two groups. It could reflect the short-term and long-term treatment efficacy separately. - We thank the reviewer for his interest on the topic and his valuable comments. At all measurement time points (not only at 12 months) there was no statistical difference between the VAS reductions. This outcome is written in the article text at p.14, l Q: Participants studied - adequately described and their conditions defined? 10. A: Yes. But the authors should state why it was difficult to recruit participants when defined the longest duration of pain pre-intervention as 6 weeks. Also, the authors should compare the baseline characteristics and treatment outcome between patients with pain no less than 6 weeks and more than 6 weeks. - We thank the reviewer for his comment. We added in Patients Characteristics Inclusion rate was slow mostly because patients were not meeting the inclusion criteria or had older fractures. p.11, l. 24 in the new text version. We consider the subgroup of patients with pain > 6 weeks <9 weeks too small to compare treatment outcome or draw any statistics, as the results will be not be clinically relevant. Q: Methods - adequately described? Complies with relevant reporting standard - Eg CONSORT for randomised trials? Ethical? A: Yes. Q: Results - answer the research question? Credible? Well presented? 11. A: Yes. But the authors should add P values in Table 1. I am very interested in whether there was any statistical difference of the duration period pre-intervention between the two groups. - We decided not to report p-values in the baseline characteristics table based on the CONSORT guidelines on reporting RCT s, and based on recommendations in various peer-reviewed publications on this topic. We refer the reviewer to a recent review on why this practice is not recommendable: de Boer, M. R., Waterlander, W. E., Kuijper, L. D., Steenhuis, I. H., & Twisk, J. W. (2015). Testing for baseline differences in randomized controlled trials: an unhealthy research behaviour that is hard to eradicate. International Journal of Behavioural Nutrition and Physical Activity, 12(1), 4. For the reviewer s interest, we conducted a Mann-Whitney U Test to compare the duration periods between groups. There was no significant difference between the groups (p=.171).

4 Q: Interpretation and conclusions - warranted by and sufficiently derived from/focused on the data? Message clear? A: Yes. Q: References - up to date and relevant? Any glaring omissions? A: Yes. No glaring omissions. Q: Abstract/summary/key messages/what this paper adds reflect accurately what the paper says? A: Yes. Other comments 12. Q1: Figure 2 caption seems wrong. The y-axis shows the VAS score rather than the number of patients. - We thank the reviewer for noting this and we have corrected the caption of figure Q2: I saw that just some of the patients with newly occurred OVCFs underwent re-intervention. What s the criteria of re-intervention? - We thank the reviewer for his comment. For clarification we added and the same inclusion criteria at p.9, l Q3: Why the rate of cement leakage is so high? - We have higher percentage of cement leakage than earlier described, because we reported even the smallest perceptible traces of cement detected on CT, as opposed to other studies where cement traces were detected using less sensitive detection techniques such as fluoroscopy or on X-ray. This is described at p.8, l.9. Please enter your name: Bin-Yan Zhong Job Title: resident Institution: Center of Interventional Radiology & Vascular Surgery, Department of Radiology, Zhongda Hospital, Southeast University, Nanjing, China Reviewer: 2 Is the article important? YES Will it help our readers to make better decisions and, if so, how? YES. BY GUIDING WHO REQUIRES CEMENT AUGMENTATION. Will the article add enough to existing knowledge? YES Does the article read well and make sense? Does it have a clear message? YES. CEMENT AUGMENTATION ONLY SUITABLE FOR LIMITED NUMBERS AND AS STATED NOT ONE SIZE FITS ALL. Originality does the work add enough to what is already in the published literature? YES Importance of the work to general readers does this work matter to clinicians, researchers, policymakers, educators, or patients? Will it help our readers to make better decisions and, if so, how? Is a general medical journal the right place for it? YES. OSTEOPOROTIC FRACTURES IS A COMMON PROBLEM. PUBLISHING IN A GENERAL MEDICAL JOURNAL WILL ALLOW POLICYMAKERS TO TAKE THE RIGHT DECISION. Research question clearly defined and appropriately answered? YES Overall design of study appropriate and adequate to answer the research question? YES Participants adequately described, their conditions defined, inclusion and exclusion criteria described? How representative were they of patients whom this evidence might affect? YES Methods adequately described? Main outcome measure clear? YES Results answer the research question? Credible? Well presented? YES Interpretation and conclusions warranted by and sufficiently derived from/focused on the data? Discussed in the light of previous evidence? Message clear? YES

5 References up to date and relevant? Any glaring omissions? YES. NO GLARING OMISSIONS. Abstract/summary/key messages/what this paper adds reflect accurately what the paper says? YES Documents in the supplemental files. Do these properly match what is in the manuscript? Do they contain information that should be better reported in the manuscript, or raise questions about the work? YES - We thank the reviewer for his positive comments. We hope that the results of this trial will help the clinician in daily practice. Please enter your name: George Ampat Job Title: Consulltant Orthopaedic Surgeon Institution: Royal Liverpool University Hospital Reviewer: Summary: This paper presents the results of a randomised controlled trial involving 180 patients randomised in a 1:1 ratio to either vertebroplasty to 1-3 acute vertebral fractures or sham procedure (lidocaine to the periosteum with mimicking of full procedure). The main eligibility criteria were focal back pain (VAS for pain intensity 5) over a fractured vertebrae for up to 9 weeks, osteopaenia (T score <-1.0), 15% height loss of the relevant vertebrae and bone oedema on MRI. The main outcome was mean reduction in VAS score during 12-month follow-up. Results showed allocation to vertebroplasty did not result in more pain relief than the sham procedure at any time point. The study has been well conducted, but the definition of vertebral fracture is questionable, and may explain their null result. - We thank the reviewer for the comment. Please see our answer at the next question (question No. 16). Main points: 16. The definition of a fractured vertebrae needs further explanation and discussion. In the methods they say it is 15%, but in Table 1 mild fractures are defined as 10-20%. They do not explain how these percentages were calculated, and this needs expanding. They also need to explain why the gold-standard morphometric-based definition (e.g. Genant) was not used, where mild fractures are 20-25% height reduction. It is generally thought that the use of 20-25% height reduction will result in a proportion of false-negatives where vertebrae are not fractured due to osteoporosis, but have short vertebral height due to other reasons such as age-related remodelling or degenerative change. The definition of mild as being 10-20% is likely to have even higher false-positives, and given that 30% of the study population had these small height reductions, perhaps they were carrying out vertebroplasty on people without fractures at all? Perhaps this explains the null results, as they were underpowered by including people without true osteoporotic fractures? - We thank the reviewer for the comment. Table 1 contains an error(!) in the definition of mild/ moderate/severe. We did use the Genant definition with the following grading: mild 15-25%, moderate 25-40% and severe >40%. This is now correctly defined in Table 1. We also added in Outcomes at p.8, l.37 the following: The assessment of the vertebral fractures was based on the Genant classification. We also added, Visual semiquantitative scoring and morphometric measurements of every vertebral compression fracture were obtained at p.8, l.37. For the reviewer s interest: Excluding patients with mild fractures resulted in similar results. The change from baseline in VAS score did not differ between the two groups (F(6,659.1)=.718, p=.635). We do not consider that this should be added in the paper. 17. As far as I am aware of, it is not known what bone oedema on MRI in the presence of 10-20% vertebral height reduction signifies. There is not enough information to be able to understand this how was bone oedema defined?

6 - Please refer also to answer No. 16. We added in Outcomes the definition of bone edema on MRI: Bone edema in the vertebral compression fracture was defined as increased signal intensity on the STIR images and decreased signal intensity on the T1-weighted images, p.8, l They do not describe how diminished bone density was identified (one of the eligibility criteria) - We added at Participants how the T-score was measured on a dual-energy X-ray absorptiometry (DEXA scan), p.6, l What is the significance of osteonecrosis mentioned in Table 1? It is not mentioned in the methods. - We added in Outcomes the definition of osteonecrosis Vertebral osteonecrosis was defined as a well circumscribed area of low signal intensity on T1-weighted MRI images, with high signal intensity on T2- weighted images at p.8, l The discussion of how these results fit in with previous literature is superficial. For example, the potential explanations of the differing results in this trial compared to VAPOUR needs expanding. - Thank you for your remark. We have addressed the potential explanations of the differing results in this trial compared to VAPOUR. Accordingly we have rewritten the Discussion, in particular section Strengths and Limitations (second paragraph), and Implications and Future Research (last paragraph). Typing errors: 21. Page 18, last two sentences appear to contradict each other - Sorry, but we see no contradiction in the last two sentences at this page. There was a significant decrease of pain in both groups, but there was no significant difference between the groups. 22. Page 20, line 4 a possibility depicted with MRI please explain - We thank the reviewer for the comment. We added such as osseous or disc degenerative disease at p.20, l.9. Please enter your name: Emma Clark Job Title: Consultant Senior Lecturer Institution: University of Bristol Reviewer: 4 Thank you for the opportunity to provide a patients review of this paper. From a patients perspective anything that reduces pain and medication has to be beneficial. As many pain medications increases risk of further falls due to their sedative effects, this can also affect general well being and confidence. 23. However, I do not understand why 'patients were asked to guess which procedure they had undergone'. (p.10, l. 34). Surely patients would have been consulted prior to the procedure as part of 'shared decision making', or 'tailor made care', (p. 22, l. 34) In my view this could affect future analysis. - Since this is a so-called blinded RCT nor the referring physician nor the patient is aware of the actual procedure (sham or cementation by randomisation). We have chosen for this scientific concept in order to determine the real added value of cementation itself and the placebo-effect. Therefore there is no place for shared decision making in this kind of research. But of course, the results of this study will be used in daily practice where shared decision making takes place between the patient and the doctor. 24. I also wonder if there were too frequent analysis points for meaningful completion by patients due to evaluation fatigue. Finally, it would have been nice to learn why the team were 'surprised by the positive response' (p.20 l.37). I feel that the paper was clearly written and do not lose sight of the positive effects for patients of reduced pain and medication. Best wishes - We thank the reviewer for the comment. In answer to questions:

7 a) It is common, like in previous vertebroplasty scientific trials, to do more analysis points during follow up. In accordance with these previous trials we decided to do the same. Neither in those previous scientific studies nor in the present trial was any such indication. b) As clinicians, despite a possible placebo effect, we did not expect such a positive treatment response in the sham group. As we stated in Discussion, p.19, l.44, the placebo effect may have played a strong role in the sham group. Please enter your name: Cheryl Berry Job Title: Patient Reviewer Reviewer: 5 In this manuscript, the authors describe the results of a randomized, double-blind, sham controlled trial of percutaneous vertebroplasty (PV) for the treatment of osteoporotic compression fractures. Vertebroplasties were performed upon 91 patients and sham lidocaine/bupivacaine injection procedures on 89 patients. The patients and their non-interventional radiology physicians were blinded to treatment type. Major inclusion criteria included 1-3 fractures, pain of up to nine weeks duration (increased from six due to slow enrollment), VAS score 5, and osteopenia. The reported mean VAS scores were 7.7 (PV) and 7.9 (sham). Analgesia with strong opiates was used by 47% (PV) and 29% (sham) of patients and with weak opiates used by 14% (PV) and 20% (sham). The primary outcome measure of VAS improvement and secondary measures of disability assessed by the Roland Morris Disability Questionnaire and Quality of Life for Osteoporosis tools did not differ significantly between the two groups at any time point up to 12 months. Non-prespecified data analyses did reveal that a significantly higher percentage of sham patients had VAS 5 at one year ( 27% vs. 16%) and also that a significantly higher percentage of sham patients had progressive vertebral height loss (45% vs. 7.8%) at one year. The authors concluded that the results of this trial do not support percutaneous vertebroplasty as standard pain treatment in patients with acute osteoporotic vertebral compression fractures. The manuscript is well written and the scientific analyses sound. The authors conclusion that percutaneous vertebroplasty is not supported by their results is, however, overly broad and does not accurately represent their narrow patient population in contrast to those from other studies that have shown significant treatment benefits from percutaneous vertebroplasty. Specific points to address: 25. Although the mean VAS scores of 7.7 and 7.9 suggest significant pain, many other factors suggest otherwise. Opiate analgesics were only used by approximately 50-60% their patients. All of their patients were treated as out patients and only 22% of patients required conscious sedation for the procedures. The reported median number of days from pain onset to the procedure (43- PV, 36-sham) and from radiographic diagnosis to the procedure (13-PV, 11-sham) indicate that most patients experienced approximately 3-4 weeks of pain prior to their imaging diagnosis. Performance of a vertebroplasty without conscious sedation or general anesthesia is very uncommon; that 78% of the authors' patients were treated in this manner suggests that their baseline pain was not sever. Pain is, of course, very subjective, but these many factors suggest their patients had only low to moderate baseline pain levels. Many patients with such fractures present with acute severe pain leading to rapid diagnosis. In most other reported series, the vast majority of patients required opiate analgesics, at least for initial pain control, and many patients required hospitalization. - We understand the reviewer s concern. We included patients with a VAS 5, which means that we included patients with moderate pain as well, as this scenario reflects better the referred population in the daily practice. Most of the patients with a vertebral compression fracture, even with a high VAS, are treated in the Netherlands as outpatients and conscious sedation is not standard. The use of opiates was

8 the same as in VERTOS II. The VAPOUR study focused on patients with a higher VAS and, as expected, the groups used more opioids (87-90%). - We suggested in the Discussion hospital inpatients with a very high VAS might benefit from an early cementation. In order to meet with the points raised by you and recommendations and wishes of several other reviewers, we have rewritten, see second paragraph Strengths and Limitations, and last paragraph of section Implications and Future Research. 26. The authors state that 156(46%) of the total eligible patients declined to participate for reasons that included treatment with open-label vertebroplasty. This suggests a selection bias toward recruitment of patients with lesser degrees of pain and disability. - We thank the reviewer for the comment. 156 patients (14%) refused to participate mostly because they choose to undergo vertebroplasty. We have mentioned that this is a limitation in our study and added to the text: This can suggest a selection bias toward recruitment of patients with lesser degrees of pain and disability p.20, l Slow initial recruitment was cited as a reason to extend the pain window from six to nine weeks. This also suggests additional selection bias. - Indeed therefore we added in Discussion in study limitations: During the trial we extended the pain window from six to nine weeks, a potential source for selection bias p.20, l The authors should emphasize the striking contrasts in the patient populations between their patients and those from the VAPOUR trial. The VAPOUR population included patients with < 6 weeks of pain (means weeks), approximately 90% of patients received opiate analgesics, only 22% of patients declined enrollment (an alternative open-label vertebroplasty was essentially unavailable within their care system), and 56-58% of patients were in-patients. To their credit, the authors do briefly remark upon some of these differences in patient populations in the paragraph preceding their conclusion. - We thank the reviewer for his important comment. We have improved the text and emphasized the striking contrasts in the patient populations following your recommendations and suggested lines. See, second paragraph section Strengths and limitation of the Discussion and last paragraph of Implications and future research of the Discussion. 29. The authors fail to adequately discuss the interesting post hoc findings of treatment benefits from vertebroplasty for significantly reducing the percentages of patients with significant persistent pain (VAS 5) and worsening vertebral height loss. Although evident only as part of the post hoc analyses, these are nevertheless very important findings. - We thank the reviewer for his comment. First of all, we added at p. 20, l.31; This confirms the assumption that cementation protects against progressive vertebral body collapse. Secondly, we added at p.20, l.35; The VERTOS II and VERTOS IV results show that the cause of adjacent level and remote fractures are most likely the result of the generalized osteoporotic disease of the osteoporotic spine and not evoked by cementation. Thirdly, we added at p. 20, l. 36; last part of strength and limitations.; In order to identify and define the predictive factors at baseline responsible for these post hoc outcomes (patients with significant persistent pain (VAS 5) and worsening vertebral height loss, at 12 months) further research is warranted. It is not inconceivable or excluded that this subgroup can be identified and distinguished at baseline as the subgroup of patients with acute osteoporotic VCFs suitable for early intervention. 30. The authors should significantly alter their conclusions to accurately reflect that percutaneous vertebroplasty failed to demonstrate a treatment benefit only in their very narrow patient population, which is not representative of the majority of patients seen in clinical practice. To do otherwise, would be disingenuous and potentially harmful to a large patient population. - We thank the reviewer for the comment. We added in Conclusion our specific group of p.21, l There is a more recent version of the authors reference number 4:

9 Barr JD, Jensen ME, Hirsch JA et al. Position Statement on Percutaneous Vertebral Augmentation: A Consensus Statement. Developed by the American Association of Neurological Surgeons(AANS) and the Congress of Neurological Surgeons (CNS), American College of Radiology (ACR), American Society of Neuroradiology (ASNR), American Society of Spine Radiology (ASSR), Canadian Interventional Radiology Association (CIRA), Society of Interventional Radiology (SIR), and the Society of NeuroInterventional Surgery (SNIS). J Vasc Interv Radiol 2014; 25(2): PMID: Thank you for pointing this out. We replaced reference no.4 with the more recent version, as you suggested. 32. I strongly suggest a companion editorial to balance the authors findings with those from other trials such as VAPOUR. As currently phrased, the authors conclusions would likely be employed to restrict patient access to percutaneous vertebroplasty. This would be a grave disservice to osteoporotic vertebral fracture patients whose characteristics do not resemble those of the authors patient population. - We do agree with the reviewer that a companion editorial should be written and published to balance our findings with those from other trials. Please enter your name: John D. Barr, MD Job Title: Professor, Radiology & Neurological Surgery Institution: Univ of Texas Southwestern School of Medicine Reviewer: 6 This is an interesting study attempting to settle the decade long controversy over the value of vertebroplasty for the treatment of pain caused by acute osteoporotic vertebral compression fractures. The authors have put together a sizable cohort, randomised it for treatment with vertebroplasty or sham and found no difference in VAS RMDQ or Qualeffo scores up to 1 year. The trail has been well designed, recognising the strong points of some of the previous trails and very well excecuted with only one protocol change when the inclusion period post vertebral fracture was extended from 6 to up to 9 weeks. The study offers valuable information for the large group of patients with an acute vertebral fracture less than 9 weeks old. For this group vertebroplasty is not better than periosteal local anaesthetic infiltration. 33. There have been 3 posthoc analyses done but the results are hardly discussed. I think these analyses could be left out since they are interesting but do not substantially add to the main message. - We thank the reviewer for the comment. We understand the reviewer s remark to send a sound message without frills. However, other comments from other reviewers have insisted to mention these important post hoc outcomes in the Discussion in order to nuance the results, without effecting the Conclusion. 34. I have some problems with the reasoning in the section implications and future research (page 21). The authors state that they continue to offer vertebroplasty to some patients. Which patients however is not clear. They state correctly that a future therapeutic pain strategy could be a combined regimen of periostal infiltration during natural healing. The authors go on : Additional cementation seems indicated only in a subgroup of patients with insufficient pain relief after this early phase However for this statement there is not any proof. The Australian sham study and the Invest study included patients up to 12 month after the fracture but did no show any benefit from cementation for these patients. For patients with a high VAS score at baseline in a clinical setting indeed there could be an indication (VAPOUR study) but it should still be shown that for this indication vertebroplasty is better than periosteal local anaesthetic infiltration. (The sham arm of this study did not get this periostal infiltration)

10 So I believe this paragraph should be rewritten and rephrased so that the implications ( periostal injections are probably as good as vertebroplasty) and future research ( are patients with an acute fracture and high VAS score in clinical setting better of with vertebroplasty than periostal injections?) are clearly stated. The phrase about personalised taylor made care can be left out. -We understand your comments and remarks. The issues mentioned are complicated, mostly because the published RCTs are not easily comparable, in particular regarding their different inclusion criteria. * The reviewer endorses that a combined therapeutic pain strategy of periosteal infiltration during natural healing might work. The reviewer refers to the sentence Additional cementation seems indicated only in a subgroup of patients with insufficient pain relief after this early phase, and states that for this statement there is not any proof, causing the argument of the Australian- and Invest results. Unfortunately we disagree, since the mentioned studies have methodological flaws, e.g. subacute fractures and fractures up to 12 months, no consistent bone edema on MR, mixed in- and outpatients. These shortcomings have also been discussed in VERTOS 2 by Klazen et al., and the reviewer. Therefore, until now, nobody can exclude a possible positive effect of vertebroplasty after 3 months. This issue will be elucidated by the VERTOS 5 RCT, including outpatient patients with painful (VAS>5) chronic VCFs only (>3 months). * In line with the reviewer we do agree that for patients with a high VAS score at baseline in a clinical setting there could be an indication (VAPOUR study), but it should still be shown that for this indication vertebroplasty is better than periosteal local anesthetic infiltration, since this has never been investigated, yet. But let s emphasize again that this is indicated for hospitalized inpatient patients only. We have added the following line: However, further research is advised to prove that vertebroplasty is better than periosteal local anesthetic infiltration in hospital inpatients, since this has never been investigated neither by VAPOUR, p. 21, l. 33, end of Implications and future research. * With regard to personalised taylor made care, we have deleted this sentence. 35. For the general reader of the BMJ in order not to lose track it would be of great interest to have a short systematic overview of the open and sham randomised studies done up to now. The focus of this review should be on patient selection (i.e. time between fracture and treatment and severity of the pain, ) the sham procedure (i.e. sometimes real sham, sometimes periosteal local anesthetic Infiltration.) and the presence or lack of a control group that represent standard medical treatment. This could also be included in an editorial comment. - We thank the reviewer for the comment. The Cochrane review from 2015, as nicely mentioned by the editors at point 4, offers a fine summary about the previous trials (added to the text of the Discussion, Strength and limitations). We agree with the suggestion that a review focused on patient selection, sham procedure, and presence or lack of a control group can be subject of a short editorial comment. We suggest to follow the recommendation of the current (W Mali) and former reviewer JD Barr; a (companion) editorial should be written and published to balance our findings with those from other trials. Some small remarks: 36. Page5 ; line 24 : It should be explained that Vertos 2 is an open label randomised controlled trial - We added, an open label randomised controlled trial at p.5, l.7, first paragraph of Introduction. 37. Page 18 : line 20 rephrase sentence starting with : in contrast to etc. - We have rephrased this sentence. p. 20, last paragraph. 38. Page 26 Flow diagram. It should be added how many patients were contributed to the trial by the different hospitals. - We added in the explanatory figure 1 legend From the 180 randomised patients, 70 were treated in Tilburg, 57 in Dordrecht, 26 in Eindhoven, and 18 in Enschede. 39. Page 20 : line1 it should be : this trial lacks an additional control group that did receive standard medical treatment. - We changed the line accordingly. Please enter your name: Willem Mali

11 Job Title: prof. dr. Institution: Imaging Division University Medical Center Utrecht The Netherlands Reviewer: 7 The authors provide the results of the VERTOS 4 study: a sham RCT investigating the effectiveness of percutaneous vertebroplasty (PVP) for painful acute (less than 9 weeks old) osteoporotic vertebral compression fractures (OVCFs). This study aimed to improve previous sham RCTs by stricter inclusion, larger patient groups, longer follow-up, injected cement volumes concordant with the guarantee of a true intervention, and no cross-overs. No benefit of PVP over the sham procedure was found during 1 year of follow-up. The study is well-designed and well executed with a thorough study design tackling important limitations of the earlier NEJM vertebroplasty trials. The manuscript is well-written. It takes tremendous effort to execute a study like this one and the authors are to be commended for this. The authors are known for their earlier extensive research on PVP by performing the landmark (open label) VERTOS 2 en 3 studies and certainly can be regarded as experts on this topic. There are no fundamentals flaws in the study and its results are robust, conclusive and clinically relevant. Regarding the study itself, I have the following questions: 40. Three post-hoc analyses were included which were not pre-specified in the study protocol. Why were specifically these analyses performed, and how many other analyses were performed which were not included in the final manuscript? - We thank the reviewer for the comment. As VAS 5 was our inclusion cut-off point, we wanted to know how many patients still had a VAS 5 one year after the treatment. Furthermore, vertebral collapse and new fractures were examined because the discussion is still pending concerning whether cementation protects against progressive vertebral body collapse or its effect on adjacent or remote vertebral bodies regarding new fractures. No additional analyses were performed. 41. For assessment of the primary outcome (between group VAS difference during 12 months of follow-up) the interaction between treatment and time was used. This, as an exploratory analysis, (correctly) assumes that the between group treatment effect may be time-dependent. However, based on previous knowledge and when examining the data and graphs, the between group difference does not appear to be time dependent. This is confirmed by the non-significant interaction term. Hence, to me it seems more appropriate to subsequently investigate the treatment effect by analyzing the data with the interaction term omitted and to provide the estimated overall between group mean difference as primary outcome measure. Although I do not expect this to really change the study conclusion, why did the authors decide otherwise? - Our analyses indicated that the groups did not differ in VAS score at baseline. Furthermore, both groups showed a significant reduction in VAS score. This reduction, however, did not differ between the groups, as indicated by the non-significant interaction between treatment and time. If the treatments do not differ at baseline and do not differ in their change over time, then the group trajectories will approximately be equal, implying that there will also be no overall effect between the two groups. For the interest of the reviewer we have conducted this test and it shows that the groups do not show an overall between group difference in mean VAS score (F(1, )=0.036, p=.849). Minor questions/comments: 42. provide estimates of between group difference in abstract (although perhaps difficult since the authors use the interaction effect as outcome measure) - We thank the reviewer for the comment. It is indeed difficult to provide the requested estimates. Therefore, they were not provided.

12 43. focal pain at the fracture site was again confirmed prior to randomization; was an additional VAS score also obtained to make sure VAS>5? - Indeed, prior to the randomisation the internist confirmed that the VAS 5 with an addition VAS score. To make this more clear we added with a VAS score 5 to p.6, first paragraph of Participants. 44. Following INVEST and the Australian trial (both 2009 NEJM trials) and the VAPOUR study (Lancet 2016), this study is the 4th sham controlled randomized trial investigating the benefit of PVP for painful OVCFs and together with these other 3 studies provides conclusive evidence for the position of PVP in treatment of acute painful OVCFs. As such, it is likely to be the final chapter regarding treatment of acute painful OVCFs with PVP: overall PVP is not superior to sham treatment and as such not indicated. Based on their experience and previous results, most notably the open label VERTOS 2 study which showed substantial benefit over conservative treatment, the authors take a more nuanced position and argue that there is a place for PVP in individual cases here a careful benefit versus risk assessment has been made together with the patient. This could be considered surprising since this is not support by the results of the present study which provides the highest level of evidence. However, besides from a understandable doctor s desire to offer active treatment, this may be also reflective of the fact the very similar but somewhat smaller VAPOUR trial in which only painful OVCFs less than 6 weeks old were included did show a significant and relevant benefit of PVP over sham treatment which sustained the entire trial length of 6 months. Besides requirement of fractures less than 6 weeks old, baseline pain 7 was required and no periosteal infiltration was performed in the sham group. Hence, it may still be possible a very selected subgroup of patients could benefit from PVP. Furthermore, the role of PVP for painful long-standing OVCFs is still unclear. In carefully selected patients with painful OVCFs with fail to respond to optimal conservative treatment i.e. those who develop a symptomatic non-union PVP may be beneficial by means of mechanical stabilization of the non-union. This mechanical effect is supported by results of pre-specified subgroup analysis of the VAPOUR trial showing an increased proportion of patients with painful OVCFS in the thoracolumbar region experiencing benefit of PVP compared to sham treatment (61% versus 13%). The authors designed the VERTOS 5 study for these group of patients which is currently recruiting patients and I look forward their results. -We thank the reviewer for his comments and interest. Please notice the answer/published paper to an earlier comment at question no. 31. In reply to your comment, we can report that VERTOS 5 (the role of PVP for painful long-standing OVCFs; symptomatic non-union OVCFs) is in its final stage. Please enter your name: Marc J Nieuwenhuijse Job Title: Clinical researcher and epidemiologist, senior resident orthopaedic surgery Institution: Leiden University Medical Center Reviewer: 8 I thank the authors for submitting this useful scientific research and would recommend its publication in the journal. My specific comments for the journal and the authors are as follows. 45. This is a well-constructed trial that further confirms that for the majority of patients with acute fragility fractures that vertebroplasty does not appear to be superior to a sham procedure, albeit a procedure that in itself may have therapeutic affect as shown by the authors. The authors rightly state that there is a still a place for the use of this treatment in carefully selected patients, however in a shared care model of decision making this does allow us to share with patients that a local anesthetic injection appears as beneficial as a vertebroplasty for giving pain relief in acute vertebral fragility fractures. There isn t a group of patients compared who received no intervention and the question would

13 be do these group of patients have a worse outcome than those who received any form of intervention. Therefore this paper doesn t allow us to conclude that this interventional treatment of any form should not be attempted under 9 weeks of symptoms. Some researchers have previously commented that treatment affect is directly related to cement volume instilled and I would welcome the authors comments on whether there was any observed affect of volume of cement instilled related to pain improvement. -We thank the reviewer for his comments. We examined the correlation between the volume of cement injected and the VAS score and found no differences. This study shows us that potentially patients with a fragility fracture with a history under 9 weeks should not undergo vertebroplasty. As the authors rightly acknowledge this trial does not help us with patients that persist with pain after 9 weeks following conservative treatment. For the majority of clinicians treating patients with fragility fractures the initial treatment is conservative, and if the pain does not improve then consideration for cement augmentation when there are persistent signal changes on MRI may be considered for treatment. Currently the scientific literature does not show us whether this group has improved pain relief over those with continued conservative care. Fragility fractures do not only cause pain, but also cause deformity and in men appear to be associated with an increased mortality from respiratory disease. No current study has shown whether long-term medical outcomes are improved by these techniques in combination with the medical treatment of osteoporosis. Similarly the observed mortality rate increases maybe related to other site fractures such as the hip, vertebral fractures probably relate to poor general health and fragility and surgical intervention in isolation is unlikely to change this. However conservative management of hip fractures is generally not accepted and potentially although not associated with any reduction in pain relief over a sham procedure not treating spinal deformity associated with fragility fractures may potentially be associated with a higher mortality in the long term. (1) Further research into long term outcomes decades after cement augmentation versus conservative care is probably the next area for assessment. Cement augmentation in terminal care and haematological malignancy should be considered separately from this treatment group, as there is separate evidence that cement augmentation is appropriate. (2) This paper is extremely useful to both patients, care givers and providers as to the place of cement augmentation in acute (less than 9 weeks) vertebral fragility fractures. However there are still questions on patient outcomes in the chronic painful fragility fracture and whether cement augmentation has a role in the prevention of long term morbidity and mortality would still appear to be areas for future research. UK Nice guidance (2016) on the use of percutaneous vertebroplasty and kyphoplasty for treating osteoporotic vertebral compression fractures states that these techniques should only be used in people who have severe ongoing pain after a recent unhealed vertebral fracture despite optimal pain management and in whom the pain has been confirmed to be at the level of the fracture by physical examination and imaging. (3) This study suggests that recent should be more than 9 weeks in duration. Certainly in my own clinical practice we have subjected patients to this technique less than 9 weeks when pain management has been associated with significant complications and agonal pain. The use of vertebroplasty under 9 weeks following this data should probably only be considered in exceptional circumstances following the publication of this trail data. 1) Ear Spine J 2011 Dec 20(12) Vertebral Fracture and cause specific mortality: a prospective population study of 3210 men and 372 women with 30 years follow up 2) Haematologica 2015 Oct 100(10): European Myeloma Network Guidelines for the management of Multiple Myeloma related Complications 3)