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Two incorrect statements? (Norman Williams, 03 February 2016)

Twice in Background the following words appear: (available from: This appears to be out of context. read full comment

Comment on: da Mota et al. Trials, 16:551

Best practices for prevention of BPD along with SAIL intervention or not (Sandesh Shivananda, 19 August 2015)

Based on previous literature on sustained inflation and other interventions during resuscitation, the effect seems to be sustained till 72 hours and not later. I am concerned about study centers focussing on initial resuscitation but loose an opportunity on concurrently implementing best practices for reduction of BPD. I would like to... read full comment

Comment on: Foglia et al. Trials, 16:95

Correction at the Acknowledgements Section  (Vincent Mok, 08 June 2015)

Dear Editor I would like to make the following important change at the Acknowledgements section.    Please change Dr Ho Tzu-leung's Foundtaion to    SH Ho Foundation supported project on Use of Chinese Herbal Medicine for Neurological Diseases.    Thank you very much for your attention. Sincerely Vincent  read full comment

Comment on: Chua et al. Trials, 16:199

Response to van Schie et al. (ALBERTO M. BOROBIA, 10 April 2015)

Antonio J. Carcas*, Alberto M.... read full comment

Comment on: Carcas et al. Trials, 13:239

Baseline incidence of aspiration is way too high (, 14 January 2015)

There are several issues here:
1) The baseline incidence of aspiration you quote (11%) is far too high. Warner's retrospective review of 172,000 patients (Anesthesiology 78:1, 56-62) showed an incidence of 0.03%. Although these were in mostly fasted patients, even if your incidence were 100-fold higher, the baseline incidence would be only by 3%. To show a change from 3% to 0% with 90% power would require 680 patients. Therefore, your study is very likely to be underpowered.
2) What is the clinical significance of the pepsin test? It will be perhaps easy to show pepsin presence, but linking this in some meaningful way to clinical aspiration with bad effects will be difficult. read full comment

Comment on: Trethewy et al. Trials, 13:17

Professional medical writers (Yvonne Yarker, 14 January 2015)

The International Society for Medical Publication Professionals (ISMPP;, a global, non-profit organization that advocates for and educates on best practices, professional ethics, and transparency in medical publishing, would like to challenge a statement made by the authors in the Discussion of this article in regard to professional medical writers: ¿if they do not do a job that satisfies the sponsors¿ marketing department, they might go out of business¿. Firstly, publication budgets are rarely held by the marketing departments of drug and device companies these days. Secondly, professional medical writers who are members of ISMPP and other relevant professional associations agree to abide by a code of ethics which, among other things, includes an obligation to ensure... read full comment

Comment on: Lundh et al. Trials, 13:146

Efficiency and effectiveness of the use of an acenocoumarol pharmacogenetic dosing algorithm versus usual care in patients with venous thromboembolic disease initiating oral anticoagulation: study protocol for a randomized controlled trial (Rianne van Schie, 14 January 2015)

R.M.F. van Schie1, T.I. Verhoef1, F.J.M van der Meer2, A. de Boer1, A.H. Maitland-van der Zee1, for the EU-PACT study... read full comment

Comment on: Carcas et al. Trials, 13:239

The coronary sinus reducer in patients with refractory angina pectoris (Yoav Paz, 14 January 2015)

Jolic Ur EM et al. erroneously compare the Neovasc coronary sinus reducer (CSR) to the Beck procedure, which has almost nothing in common with the Neovasc CSR. Actually this statement can be concluded by reading references 6-10 in Jolic Ur EM et al. study protocol.[1] In the 1940s, Dr Claude Beck described two types of coronary sinus (CS) interventions.[2-4] The Beck I procedure consisted of 4 components: 1) external surgical narrowing of the CS; 2) abrading both the epicardium and inner pericardium (some kind of neurectomy procedure that was used for the treatment of refractory angina pectoris in those days); 3) spilling of powdered asbestos and 5% aqueous trichloracetic acid on the epicardium; 4) placing mediastinal fat over the treated epicardium. The Beck II procedure consisted of 2... read full comment

Comment on: Jolicœur et al. Trials, 14:46

Full analysis plan is now available (Martin Dennis, 09 January 2015)

A full description of the analysis plan is now available at

This analysis plan was prepared by Profs Martin Dennis, Peter Sandercock, Gordon Murray and John Forbes. It was prepared before recruitment was complete and was written without knowledge of any interim analyses which identified the separate treatment groups. The trial statistician, Catriona Graham, who prepared the interim analyses for the DMEC was not involved in the preparation of this analysis plan. This plan should be read in conjunction with this article and the full protocol available at read full comment

Comment on: Dennis et al. Trials, 13:26

Erratum (References) (Christopher Etherton-Beer, 19 December 2014)

Re: Trials 2010, 11:63 (doi:10.1186/1745-6215-11-63) Erratum (References)

The reference to Mann 2000 (Reference 10) on page 3 is incorrect. The reference should be to Zimmerman 2005 (Reference 15).

The authors apologise for this error. read full comment

Comment on: Beer et al. Trials, 11:63

Typographical correction for inclusion criterion  (Leanne Williams, 17 December 2014)

On Page 3, the Inclusion criterion for total score on the HRDS17 should be HRDS17 ≥ 16 read full comment

Comment on: Williams et al. Trials, 12:4

Concern over lack of statistical adjustment for clustering (Gordon Doig, 15 December 2014)

I am very concerned that lack of statistical adjustment for clustering has led to a false positive result in this... read full comment

Comment on: Savolainen-Kopra et al. Trials, 13:10

Special Acknowledgement (Sheraz Nazir, 13 October 2014)

The authors would like to especially acknowledge the great effort and contribution of Lorraine Shipley as the Trial Manager of the REFLO-STEMI Trial. read full comment

Comment on: Nazir et al. Trials, 15:371

The validity of using subjective outcome measures as primary outcomes is questionable in such a trial (Tom Kindlon, 29 July 2014)

Crawley and colleagues suggest dropping school attendance as a primary outcome from the full study, and replacing it with self-report outcomes "such as the SF-36 or the Chalder Fatigue Scale" and using "school attendance as a secondary outcome"(1). And indeed, this is what they have done with the full study which has two primary outcome measures: "Chalder Fatigue Scale at 6 months" and "SF 36 physical function short form at 6 months"(2). I question the wisdom of using self-report measures as primary outcomes for such a... read full comment

Comment on: Crawley et al. Trials, 14:415

There might be some minor mistake of this publication (xin wang, 29 July 2014)

Page 3, the Inclusion criteria should be Total HRDS17≥16,NOT HRDS17≤16 read full comment

Comment on: Williams et al. Trials, 12:4

Searching and analysing registered clinical trial data more feasible wirh the WHO ICTRP (Roderik Viergever, 28 July 2014)

I read this article with interest. It is a good example of the opportunities that clinical trials registration offers for monitoring countries’ health research portfolios and informing future health research... read full comment

Comment on: Raftery et al. Trials, 13:140

Mammography screening increases non-breast cancer mortality (, 05 December 2013)

Erpeldinger et al. used the randomised trials to find out whether mammography screening increases non-breast cancer mortality. As we have explained in our Cochrane review (1), to which the authors refer, this cannot be done. One of the problems is that assignment of cause of death was biased in these trials, but the most important problem we describe in our review is this... read full comment

Comment on: Erpeldinger et al. Trials, 14:368

Response to comment by Hamilton et al. (Andreas Lundh, 22 November 2012)

`Owing to technical issues with the Trials comments page, the authors were unable to post this comment when originally submitted on the 5th... read full comment

Comment on: Lundh et al. Trials, 13:146

Addressing the implication made by the authors that if medical writers "do not do a job that satisfies the sponsors' marketing department, they might go out of business." (Cindy Hamilton, 20 September 2012)

To the... read full comment

Comment on: Lundh et al. Trials, 13:146

Efficacy due to alcohol or something else in the mouthwash composition? (Dirk Lachenmeier, 27 March 2012)

As it was previously noted, a considerable industry bias in mouthwash-related research exists [1]. Therefore, it would be interesting to know the sponsor of the study and if the sponsor was affiliated with any of the mouthwash brands under... read full comment

Comment on: Marchetti et al. Trials, 12:262

Comparing apples and oranges (Joselita Salita, 21 July 2011)

I appreciate the goals of Nairy et al.'s paper. However, their primary objective was incomplete which made them design an experiment which compared apples and oranges. The three groups could only be partially compared: group 1 vs 2 and 1 vs 3, which in the end, could not support their conclusions.

In order to assess the efficacy of in-situ gels in treating OPC, one compares in-situ gels with a placebo or a comparator (in this case, flucanozole tablets) or both among one patient type. Having two types of patients, with one type incompletely represented was a major flaw. The choice of comparing responses among HIV/AIDS patients as a patient type was also not a good idea due to confounding effects. The resulting „good clinical response“ of HIV patients after 21... read full comment

Comment on: Nairy et al. Trials, 12:99

To the Editor (Dirk Kuhlmann, 23 June 2011)

The study showing an in situ gel formulation is an interesting approach for treatment of OPC. The clinical study data presented by Nairy et al. is poorly organized and confusing.

The reliability of the results is questionable due to incomplete outcome data and selection bias from randomization based on clinical evaluation. The three study groups are only partially comparable. As group II is missing a control group, the data is not supportive of the aim of the study.

Severity of signs and symptoms are mild to absent according to table 3. An effect of treatment on moderate to severe cases is not presented. Patient demographics of group 3 are diverse with a possible confounding bias associated with a large variance in CD4 count.

The primary endpoints are not... read full comment

Comment on: Nairy et al. Trials, 12:99

Systematizing the analysis of effect heterogeneity requires rethinking some fundamentals (James Scanlan, 01 June 2011)

The article by Gabler et al.[1] questions the soundness of epidemiological literature’s reporting and analysis of heterogeneity of treatment effects (HTE) and calls for greater attention to HTE issues and more systematic analysis of such issues.

But the goals the authors seek cannot be achieved without reconsideration of certain fundamentals of subgroup analysis. Standard approaches to such analyses are based on an assumption that absent HTE all subgroups will experience equal proportionate changes in outcome rates (i.e., the same rate ratio across different baseline rates) and that HTE is observed in those cases where equal proportionate changes are not found. That assumption, however, is demonstrably unsound for the simple reason that it is not possible for a factor... read full comment

Comment on: Gabler et al. Trials, 10:43

Assessing heterogeneity of treatment effects in light fundamental statistical tendencies (James Scanlan, 26 May 2011)

The article by Kent et al.[1] provides useful guidance on the reporting of results by subgroup. But the article suffers from the common assumption that the absence of a subgroup effect (heterogeneity) is reflected by equivalent relative risk reductions across subgroups. It is not logical to regard equivalent relative risk reductions as somehow normal (i.e., as reflecting the absence of a subgroup effect) for the simple reason that it is not possible for a factor to cause equal relative reductions in an outcome for groups with different base rates while causing equal relative increases in the opposite outcome for those groups.

The point can be illustrated with figures in Table 1 of Kent et al., which shows the same 25% relative risk reduction of an adverse outcome for an... read full comment

Comment on: Kent et al. Trials, 11:85

Erratum: minor error (Andrew Vickers, 30 November 2010)

In the text of our protocol, we gave an incorrect affiliation to JianPing Liu. He is not, as we suggested, affiliated with the Chinese Cochrane Center, but is Director of the Centre for Evidence-Based Chinese Medicine, Beijing University of Chinese Medicine. The last sentence of the "Search strategy for identification of studies" section should therefore read:

Chinese trials will be identified by a separate process: Jianping Liu of the Centre for Evidence-Based Chinese Medicine, Beijing University of Chinese Medicine, will use that institution's resources to identify Chinese trials of acupuncture for chronic pain that involved full allocation concealment.
read full comment

Comment on: Vickers et al. Trials, 11:90