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I'd like to commend you on running a large RCT on such an important topic (assessing the purported effectiveness of concussion-reduction technologies). Unfortunately I have some concerns about some aspects of your data and analysis, particularly the as-treated analysis in Table 4and your reported adherence numbers. I am hoping you can clarify these concerns and re-do parts of your analysis.
1. In the as-treated analysis you have a very strange result. Your multivariate risk ratio (which is actually a rate ratio) is 0.63 for everyone overall, 0.64 for females, and 0.93 for males. The result for everyone should be between the results for males and females. Can you please clarify how you got these results, including the exact model(s) you used and how you calculated the rate ratios? Did you use a group*sex interaction term to get the sex-specific results?
2. How you defined the as-treated group is concerning. You state that you only re-classified a subject if they spent >50% of their time in their non-assigned group OR if they were concussed while in their non-assigned group. This approach will bias the results of your as-treated analysis as you are deliberately misclassifying the AEs of people who do not get hurt and the non-concussed AEs of those who do. You need to classify every AE, rather than each athlete, as headgear or no headgear and repeat the as-treated analysis. Otherwise this analysis is highly questionable and...
I'd like to commend you on running a large RCT on such an important topic (assessing the purported effectiveness of concussion-reduction technologies). Unfortunately I have some concerns about some aspects of your data and analysis, particularly the as-treated analysis in Table 4and your reported adherence numbers. I am hoping you can clarify these concerns and re-do parts of your analysis.
1. In the as-treated analysis you have a very strange result. Your multivariate risk ratio (which is actually a rate ratio) is 0.63 for everyone overall, 0.64 for females, and 0.93 for males. The result for everyone should be between the results for males and females. Can you please clarify how you got these results, including the exact model(s) you used and how you calculated the rate ratios? Did you use a group*sex interaction term to get the sex-specific results?
2. How you defined the as-treated group is concerning. You state that you only re-classified a subject if they spent >50% of their time in their non-assigned group OR if they were concussed while in their non-assigned group. This approach will bias the results of your as-treated analysis as you are deliberately misclassifying the AEs of people who do not get hurt and the non-concussed AEs of those who do. You need to classify every AE, rather than each athlete, as headgear or no headgear and repeat the as-treated analysis. Otherwise this analysis is highly questionable and should be removed from the paper.
3. You report extremely high adherence (99.53%). Is this taking into account any non-adherence or only non-adherence from students not adhering for a majority of their AEs or suffering a concussion while non-adherent? It would be very helpful to see total non-adherence since it sounds like your ATs reported that? I would like to emphasize again that this total non-adherence is what should be used in your as-treated analysis.
If 0.47% is the total non-adherence for all participants, would you be willing to share some strategies you used to secure such great adherence?
4. Finally, it seems there is an extremely high rate of concussions among the non-adherent AEs. Per Table 4 and the text of your paper, there were at least 7 concussions among the 711 non-adherent AEs for a rate of 9.85 per 1,000 AEs. For the adherent group this leaves 123 concussions in 150,466 AEs for a rate of 0.82 per 1,000 AEs. This suggests the rate of concussions in the non-adherent was at least 12-fold that in the adherent (regardless of whether these involved wearing headgear or not). This is a very strong effect. Do you have any explanation for this vast difference? It is possible that this difference will shrink or disappear if you correctly count all non-adherent AEs as non-adherent.
Thank you again for conducting these trial and for your kind attention to these questions!
We would like to thank you for your insightful and interesting comment.
Regarding the first point, we presented the 28.5% to illustrate the relative difference in total absolute fat (kg) change between interventions, so the reader could have information about the relative difference between groups. We would like to highlight that it was only possible to perform this analysis using the within group changes, since the change between group analysis was showed in absolute values.
About the second point, it was not our purpose to analyse lean body mass; however, we agree that this topic is very important for health and athletic performance purposes. This is an unanswered question and we are performing studies to test the effects of interval training on lean body mass to help shedding light in the topic.
In this article the authors discuss their analysis of 21 female and 22 male athletic events. Testing all 43, they find 3 events significant with p<0.05. When testing 43 events, the expectation is that a well-calibrated statistical test will produce 2 false positives with random data, on average, due to the definition of the p-value. The odds of producing 3 false positives are also rather high; for normally distributed simulated data under the null, I found 3 or more false positives approximately 1/3 of the time such an analysis is performed, see here for a simulation notebook: https://github.com/davidasiegel/False-Positive-Rate-for-Multiple-Tests-i....
This is why adjustments for multiple comparisons needs to be performed. It was neglected in their initial study and neglected again in this study. In the 2017 study they state, "These different athletic events were considered as distinct independent analyses and adjustment for multiple comparisons was not required." This doesn't make sense to me; if the analyses are distinct, then all the more reason to correct for multiple comparisons. If a Bonferroni correction were performed, none of the p-values would test significant at the level of the study (p<0.05/43 = 0.001). Therefore I do not see why there is any reason to reject the null hypothesis for any of these results.
In this article the authors discuss their analysis of 21 female and 22 male athletic events. Testing all 43, they find 3 events significant with p<0.05. When testing 43 events, the expectation is that a well-calibrated statistical test will produce 2 false positives with random data, on average, due to the definition of the p-value. The odds of producing 3 false positives are also rather high; for normally distributed simulated data under the null, I found 3 or more false positives approximately 1/3 of the time such an analysis is performed, see here for a simulation notebook: https://github.com/davidasiegel/False-Positive-Rate-for-Multiple-Tests-i....
This is why adjustments for multiple comparisons needs to be performed. It was neglected in their initial study and neglected again in this study. In the 2017 study they state, "These different athletic events were considered as distinct independent analyses and adjustment for multiple comparisons was not required." This doesn't make sense to me; if the analyses are distinct, then all the more reason to correct for multiple comparisons. If a Bonferroni correction were performed, none of the p-values would test significant at the level of the study (p<0.05/43 = 0.001). Therefore I do not see why there is any reason to reject the null hypothesis for any of these results.
Performing a series of tests and then re-testing the subset of events with the most significant results is also poor statistical practice that doesn't add meaning to the study.
In conclusion, taking into account the total number of tests that were performed (43), the results fail to be significant at the level of the study.
For readers who are following the debate about how training load may relate to injury, Dr Johann Windt considers the implication of the correlation that is pointed out here. Thanks to all the authors. k2
The study raises two questions that one of the authors might be able to help with:
First, the authors report both within group and between group changes in body fat in the abstract. But it is unclear why the authors chose the within-group changes (28% fat loss) as the study conclusion than the between-group change.
The within group change showed a fat loss of 0.45 kg (28%) in favor of interval training (IT), while the between-group changes showed a large difference of 2.28 kg of fat loss in favor of IT. Considering the large difference in fat loss, and some studies recommending to avoid within group differences in meta-analysis, it would be helpful if the authors could comment on this.
Second, maintaining lean body mass (LBM) is one of the primary reasons to include exercise as part of a weight loss strategy. So it is not clear why the authors chose not to include lean body mass as one of the outcomes. It would have certainly helped the reader to make a decision regarding the choice of exercise for weight loss.
Finally, congratulations to all the authors for asking a very relevant question!.
We thank Freke et al. (1) for their systematic review about physical impairments in patients with symptomatic femoroacetabular impingement, nonetheless we have some remarks about methods and results of the article, in particular for range of motion (ROM) outcome.
A meta-analysis of ROM was performed without reporting an overall estimate. Taking into account the amount of studies included and their information, a meta-analysis should have been accomplished. Nonetheless, authors concluded that individuals with symptomatic FAI demonstrated no difference in hip ROM in any direction of movement. This conclusion was unexpected taking into account the findings reported in the primary studies included), and in the previous systematic review published in 2015 (2), that showed instead a reduced ROM.
This discrepancy in literature is already discussed by the Warwick agreement (3), where authors stated that “the evidence on hip range of motion (ROM) in FAI syndrome is surprisingly contradictory” due to contrasting published systematic reviews (1) (2).
Therefore, we checked the accuracy of results reported, analyzing the data reported for every movement assessed in primary studies comparing those reported in this systematic review. We noted some issues in the represented forest plots.
Firstly, some included studies (4), (5), (6), (7) were reported twice in the meta-analysis for different times points or reporting double data of the same patients obtained by two...
We thank Freke et al. (1) for their systematic review about physical impairments in patients with symptomatic femoroacetabular impingement, nonetheless we have some remarks about methods and results of the article, in particular for range of motion (ROM) outcome.
A meta-analysis of ROM was performed without reporting an overall estimate. Taking into account the amount of studies included and their information, a meta-analysis should have been accomplished. Nonetheless, authors concluded that individuals with symptomatic FAI demonstrated no difference in hip ROM in any direction of movement. This conclusion was unexpected taking into account the findings reported in the primary studies included), and in the previous systematic review published in 2015 (2), that showed instead a reduced ROM.
This discrepancy in literature is already discussed by the Warwick agreement (3), where authors stated that “the evidence on hip range of motion (ROM) in FAI syndrome is surprisingly contradictory” due to contrasting published systematic reviews (1) (2).
Therefore, we checked the accuracy of results reported, analyzing the data reported for every movement assessed in primary studies comparing those reported in this systematic review. We noted some issues in the represented forest plots.
Firstly, some included studies (4), (5), (6), (7) were reported twice in the meta-analysis for different times points or reporting double data of the same patients obtained by two instruments to measure ROM. The number of observations in the analysis should match the number of individuals (unit) that are randomized or allocated: reporting twice data from the same patients is not appropriate, resulting in an error of unit of analysis inflating the sample size. Secondarily, two studies were included in the meta-analyses selecting an inappropriate control group. In particular, the control group in one study was represented by post-surgery impingement population instead of the healthy control, even if the displaced forest plot indicated the comparisons “pre versus control” (8). Analogously, an inappropriate population was selected in another study (6) for the femoroacetabular group where authors chose arbitrarily data from the subgroup of patients with cam impingement, while they should have chosen data reported from combined cam or pincer impingement, since the aim of the review was to measure physical impairment in patients with any kind of FAI.
We are confident with data published in this review of Freke et al (1): checking data from all primary studies we confirmed that data were correctly reported by authors in tables 1 and 2, however inconsistency between data extraction and analysis is present. It is unclear the estimate and related confidence intervals reported in each forest plot. Reasons could be related to authors obtain missing outcome data from contacting primary authors, nevertheless, this information should be transparently reported in the systematic review. For every direction of movement analyzed, the confidence intervals appear to be too large and, in some cases, the SMD calculated seemed to be wrong, making non-significant some of the significant differences published in the primary studies.
Considering the errors in selective reporting and aggregation of data we claim the conclusion of the review about ROM is not correct. Even if the authors did not show the diamond of the overall results in forest plots, they concluded that there is no statistically significant deficit in ROM in any plane of movement, and visually impressed stakeholders by the forest plots that sustain this conclusion. Anyway, we correctly re-run the analyses and we found that there is a statistically significant ROM deficit in flexion, abduction, external rotation and internal rotation in patients with FAI versus controls.
Errors in published systematic reviews are possible (9), but they can limit validity of conclusions of systematic reviews and resulting statements, agreements or clinical guidelines. We understand that peer-reviewers cannot check every calculation or data analysis but the importance of meta-analysis in the hierarchy of evidence need high level of attention and hopefully technical support to the reviewers to avoid relevant mistakes. At the same time, to improve transparency and help the review process, Journals should require authors to submit the raw data and to share the dataset used for the analyses, when they are not reported in the forest plot.
References
1. Freke MD, Kemp J, Svege I, Risberg MA, Semciw A, Crossley KM. Physical impairments in symptomatic femoroacetabular impingement: A systematic review of the evidence. Br J Sports Med. 2016;50(19):1180.
2. Diamond LE, Dobson FL, Bennell KL, Wrigley T V., Hodges PW, Hinman RS. Physical impairments and activity limitations in people with femoroacetabular impingement: A systematic review. Br J Sports Med. 2015;49(4):230–42.
3. Griffin DR, Dickenson EJ, O’Donnell J, Agricola R, Awan T, Beck M, et al. The Warwick Agreement on femoroacetabular impingement syndrome (FAI syndrome): An international consensus statement. Br J Sports Med. 2016;50(19):1169–76.
4. Nussbaumer S, Leunig M, Glatthorn JF, Stauffacher S, Gerber H, Maffiuletti NA. Validity and test-retest reliability of manual goniometers for measuring passive hip range of motion in femoroacetabular impingement patients. BMC Musculoskelet Disord. 2010;11(194).
5. Bedi A, Dolan M, Hetsroni I, Magennis E, Lipman J, Buly R, et al. Surgical Treatment of Femoroacetabular Impingement Improves Hip Kinematics. Am J Sports Med. 2011;39(1 Suppl):43–9.
6. Harris-hayes M, Mueller MJ, Sahrmann SA, Bloom NJ, Steger-may K, Clohisy MAJC, et al. Persons With Chronic Hip Joint Pain Exhibit Reduced Hip Muscle Strength. J Orthop Sport Phys Ther. 2014;44(11):890–8.
7. Audenaert EA, Peeters I, Vigneron L, Baelde N, Pattyn C. Hip Morphological Characteristics and Range of Internal Rotation in Femoroacetabular Impingement. Am J Sports Med. 2012;40(6):1329–36.
8. Kubiak-Langer M, Tannast M, Murphy SB, Siebenrock K a, Langlotz F. Range of motion in anterior femoroacetabular impingement. Clin Orthop Relat Res [Internet]. 2007 May [cited 2012 Mar 9];458(458):117–24. Available from: http://www.ncbi.nlm.nih.gov/pubmed/17206102
9. Yip R, Islami F, Zhao S, Tao M, Yankelevitz DF, Boffetta P. Errors in systematic reviews : an example of computed tomography screening for lung cancer. Eur J Cancer Prev. 2014;23(i):43–8.
I would like to congratulate the British Journal of Sports Medicine for the publication of the study ‘The Adductor Strengthening Programme prevents groin problems among male football players: a cluster-randomised controlled trial’ conducted by Harøy et al.[1]. The study investigated the effect of the adductor strengthening programme on the prevalence of groin problems among football players. The findings are incredibly important for the development of sports medicine because of their clinical relevance.
Regarding the methodology of this study, rather than giving criticism, I would like to suggest the authors if they can provide additional information or even a follow-up article on the game performance of the football teams involved in this study. As mentioned in the article, the authors have considered the groin pain causing time loss, decreasing participation or performance of the players [1]. Meanwhile, the previous study literally found that a lower incidence rate was strongly correlated with the number of goals, games won and even team ranking position [2,3]. Therefore, readers are interested whether the performance could be improved too since the results showed a significant reduction in the prevalence of groin pain in the players.
Similar studies have been conducted to investigate the effect of a specific strength training programme on players’ injury prevalence and individuals’ performance [4]. However, no data was included to refl...
I would like to congratulate the British Journal of Sports Medicine for the publication of the study ‘The Adductor Strengthening Programme prevents groin problems among male football players: a cluster-randomised controlled trial’ conducted by Harøy et al.[1]. The study investigated the effect of the adductor strengthening programme on the prevalence of groin problems among football players. The findings are incredibly important for the development of sports medicine because of their clinical relevance.
Regarding the methodology of this study, rather than giving criticism, I would like to suggest the authors if they can provide additional information or even a follow-up article on the game performance of the football teams involved in this study. As mentioned in the article, the authors have considered the groin pain causing time loss, decreasing participation or performance of the players [1]. Meanwhile, the previous study literally found that a lower incidence rate was strongly correlated with the number of goals, games won and even team ranking position [2,3]. Therefore, readers are interested whether the performance could be improved too since the results showed a significant reduction in the prevalence of groin pain in the players.
Similar studies have been conducted to investigate the effect of a specific strength training programme on players’ injury prevalence and individuals’ performance [4]. However, no data was included to reflect the impact on the teams' performance. Specifically, a unique methodological advantage of Harøy et al. ‘s RCT was based on both individuals and teams ie. 18 teams in the intervention group versus 17 teams in the control group [1]. If there were no significant changes in other factors between the two groups throughout the study period, it is possible to generate more statistics on the teams’ performance for comparison after the intervention.
In summary, these contributions are intended to explore additional data of the study to improve this valuable manuscript even further. Because I believe that this study will have a direct impact on clinical practices, being a reference for deciding the most appropriate injury prevention programme, potentially performance enhancement as well, in sports medicine and the industry.
Reference
1 Harøy J, Clarsen B, Wiger EG, et al. The Adductor Strengthening Programme prevents groin problems among male football players: A cluster-randomised controlled trial. Br J Sports Med 2018;:145–52. doi:10.1136/bjsports-2017-098937
2 Eirale C, Tol JL, Farooq A, et al. Low injury rate strongly correlates with team success in Qatari professional football. Br J Sports Med 2013;47:807–8. doi:10.1136/bjsports-2012-091040
3 Hägglund M, Waldén M, Magnusson H, et al. Injuries affect team performance negatively in professional football: An 11-year follow-up of the UEFA Champions League injury study. Br J Sports Med Published Online First: 2013. doi:10.1136/bjsports-2013-092215
4 Barengo N, Meneses-Echávez J, Ramírez-Vélez R, et al. The Impact of the FIFA 11+ Training Program on Injury Prevention in Football Players: A Systematic Review. Int J Environ Res Public Health 2014;11:11986–2000. doi:10.3390/ijerph111111986
Many of you will be familiar with The BMJ and its popular 'Rapid Responses'. Because we are a sister journal to The BMJ (and part of the same publishing company of course) we have the same Platform and we encourage you to use it.
Why is this in BJSM? In general, it is best to have papers go through peer review in the most relevant journal to their subject matter to ensure that the production team is well placed to find suitable editors and reviewers.
Letter to the Editors
Br J Sports Med
J Obstet Gynecol Canada
Oslo, Nov 23rd 2018
Comment and questions to Mottola et al (2019): 2019 Canadian guideline for physical activity throughout pregnancy
We have read the Canadian guideline for physical activity throughout pregnancy with great interest. We note that the guideline team have made their recommendation regarding pelvic floor muscle training (PFMT) based on evidence from a systematic review from the same research group (Davenport et al 2018). The main results of this review are in line with the latest Cochrane review (Woodley et al 2017) on the same topic; while there are some methodological differences and variations in which studies were included or not (two of the largest studies on PFMT was left out from the Davenport review; Mørkved et al 2003 and Stafne et al 2012), the findings in terms of size and precision of effect are similar, although Davenport et al used odds ratio and Woodley et al used risk ratio for their summary statistic. Davenport et al reported that PFMT gave a 50% reduction in prenatal UI and a 35% reduction in postnatal UI, but the guideline team concluded a “weak recommendation” for PFMT because UI was not rated as a "critical outcome" and the evidence was of "low quality". We find this conclusion at odds with the evidence and the interpretation of the evidence based on the guideline team’s own criteria.
The Canadian guideline grades...
Letter to the Editors
Br J Sports Med
J Obstet Gynecol Canada
Oslo, Nov 23rd 2018
Comment and questions to Mottola et al (2019): 2019 Canadian guideline for physical activity throughout pregnancy
We have read the Canadian guideline for physical activity throughout pregnancy with great interest. We note that the guideline team have made their recommendation regarding pelvic floor muscle training (PFMT) based on evidence from a systematic review from the same research group (Davenport et al 2018). The main results of this review are in line with the latest Cochrane review (Woodley et al 2017) on the same topic; while there are some methodological differences and variations in which studies were included or not (two of the largest studies on PFMT was left out from the Davenport review; Mørkved et al 2003 and Stafne et al 2012), the findings in terms of size and precision of effect are similar, although Davenport et al used odds ratio and Woodley et al used risk ratio for their summary statistic. Davenport et al reported that PFMT gave a 50% reduction in prenatal UI and a 35% reduction in postnatal UI, but the guideline team concluded a “weak recommendation” for PFMT because UI was not rated as a "critical outcome" and the evidence was of "low quality". We find this conclusion at odds with the evidence and the interpretation of the evidence based on the guideline team’s own criteria.
The Canadian guideline grades evidence as either “strong or weak based on the (1) balance between benefits and harms, (2) overall quality of the evidence, (3) importance of outcomes (ie, values and preferences of pregnant women), (4) use of resources (ie, cost), (5) impact on health equity, (6) feasibility and (7) acceptability. A strong recommendation is one where “Most or all pregnant women will be best served by the recommended course of action” and a weak recommendation is one where “Not all pregnant women will be best served by the recommended course of action; there is a need to consider other factors such as the individual’s circumstances, preferences, values, resources available or setting. Consultation with an obstetric care provider may assist in decision-making.”
We disagree with how PFMT has been classified in relation to these criteria and would like to question and comment on the following:
1.Balance between benefits and harms: the effect size of antenatal PFMT for prevention of UI is moderate and there are no harms of PFMT, so this would be in favor of a strong recommendation. In addition, many of the studies in the Davenport et al (2018) review did not compare PFMT with no exercise/untreated controls, rather the control groups typically also had some advice or instruction in PFMT as part of ‘routine’ care. Such trials are likely to under- rather than overestimate the effect of PFMT, suggesting the true effect size may be larger than that calculated by Davenport et al (2018).
2.Overall quality of the evidence: There are three issues to consider here:
a. Research design. There are sufficient numbers of RCTs evaluating effect of PFMT on UI during pregnancy to do meta-analyses without including cohort studies with lower internal validity. The Davenport review (2018) referred to cohort studies and showed that general exercise (not PFMT) may increase the odds of developing UI. Aerobic exercise usually includes high impact activities (jumping and running). Numerous studies (Bø 2004, Nygaard & Shaw 2016) have shown that high impact activities are associated with UI, therefore this combination is likely to be provocative of UI and mask a stand-alone effect of PFMT on reduction of UI. Studies on aerobic exercise can therefore not be expected to have a positive effect on UI and should not be recommended to be combined with studies on PFMT. In all reports in this area general exercise /physical activity needs to be separated from specific PFMT, in order not to confuse the readers.
b. Risk of bias. All the trials are inevitably at risk of bias through an inability to blind participants and providers, yet this would be the same for all forms of physical activity (yoga) and should not affect the rating of PFMT more than other exercise. The included trials are also the usual ‘mixed bag’ of less and more robust trials. While most studies are small to moderate in size it seems likely that the true underlying effect is within the existing confidence limits of the effect estimate (Herbison et al 2011). Both in the Cochrane (Woodley et al 2017) and the Davenport et al (2018) reviews the upper limits of the confidence intervals suggest clinically important reduction in UI.
c. Statistical heterogeneity. For PFMT, a plausible explanation for statistical heterogeneity is the different training doses and supervision (Hay-Smith et al 2011). We agree that more work is needed to find a ‘cut off’ for effectiveness in PFMT delivery and dose, but in the meantime there are certainly robust trials with well described interventions demonstrating clinically significant effect that are suitable models for application in practice.
3. Importance of outcome: UI is a prevalent (>30%) and bothersome condition reducing QoL and especially participation in physical activity (Nygaard et al 2005, Hamid et al 2015), and therefore important to prevent. In the Canadian guideline it is stated that prior to convening the panel, "10 pregnant women were recruited by convenience sampling and invited to provide input on the perceived benefits and harms of physical activity, and to identify pregnancy outcomes that were most important to them." Studies consistently finds women perceive UI as stigmatizing and at the same time ‘normal’ for parous women, and UI is a topic they are reluctant to talk about (Hamid et al 2015). Postpartum the dominant view of women is that of ‘if only I’d known then what I know now’, and ‘I wish someone had told me about UI, and taught me how to do PFMT properly’ (Mason et al 2001, Mason et a 2001, Neels et al 2016). If the 10 pregnant women in the expert group were continent, not aware that they might develop incontinence after birth and were more concerned about other common maternity conditions or the health of the babies, UI may not have reached their attention. We are surprised that specialized women's health physiotherapists who are the experts in this field both in high quality research and clinical practice, were not included in the panel nor as experts.
4. Use of resources: PFMT is already part of ante-and postnatal health care in most developed countries. PFMT has proved to be effective as part of group training for women and can therefore be administered at low cost to the health system.
5. Impact of health equity: Not informing or providing PFMT to pregnant women creates inequity as failure to prevent UI in pregnancy means that women are potentially set up for many years of UI symptoms with all the consequent effects on self-esteem, withdrawal from physical activity, not playing with their children, the cost of buying products and laundry and the cost of physiotherapy and surgery.
6. Feasibility: PFMT has successfully been incorporated in comprehensive exercise classes since 1986 (Bø et al 1990, Mørkved et al 2003, Stafne et al 2012).
7. Acceptability: PFMT research is firmly on the side of acceptability. Studies show that women want to do PFMT as first line treatment, but they must be informed about why and how they should do it (Mason et al 2001, Mason et al 2001). The long-term effect of PFMT is, as for all exercise interventions, dependent on maintenance of training. There are challenges with long term adherence/attrition from all forms of exercise/physical activity programs, and this is NOT a specific nor more pronounced problem for PFMT. Again, this is not an argument for assigning PFMT a weak recommendation.
In summary, it appears the guideline panel has, perhaps in deciding on a weak recommendation, over-emphasized concerns about quality of evidence (in which other areas of exercise in medicine are there more RCTs showing clinically relevant effect?), and may not have ‘heard’ how bothered women are about the problem of UI. Most, or all, pregnant women would benefit from PFMT during pregnancy to prevent UI because: PFMT does prevent UI in late pregnancy, postpartum, and potentially for life (as well as preventing pelvic organ prolapse), it does no harm, women would do PFMT if they knew why it was important (but the system fails them by not giving them this information), women who do leak experience significant bother, and the training can be incorporated with other physical activity to maximize gains from time spent in exercise. The Canadian guidelines' weak recommendation appears inconsistent with the evidence and positive impact of existing research.
Strong recommendation for yoga?
We further question the evidence for the "strong recommendation" and "high quality evidence" that adding yoga and gentle stretching is beneficial. For which conditions is yoga beneficial during pregnancy? It would seem that yoga/ gentle stretching classes would indeed have the same cost and feasibility/ equity/ acceptability concerns as group training of the PFM.
Diastasis recti abdominis
Why is diastasis recti abdominis considered a critical outcome? There is no scientific evidence that this causes any harm. The guidelines refer to the systematic review of Davenport et al (2018 b). They conclude that there is no relationship between prenatal exercise and diastasis. However, the guideline states that continuing aerobic exercise (walking) is associated with less odds of development of diastasis. Based on which studies? Neither Sperstad et al (2016) nor Fernandes de Mota et al (15) found such associations.
The guideline recommends that women with a diastasis postpartum should avoid curl-ups and refer to Mota et al (2015) to support this statement. However, Mota et al (2015) found the contrary; abdominal crunch narrows the inter-rectal distance and indrawing opens the gap. This has now been supported by several studies.
In conclusion, we are concerned that how the Canadian guideline group have defined quality of evidence and weak and strong recommendations, may mislead pregnant women and heath care providers to believe that there is weak scientific evidence for prevention and treatment effects of PFMT for UI. This may discourage pregnant women from starting or continuing PFMT in a very important period to prevent and treat the condition. The guideline group may have - inadvertently – through issuing a weak recommendation for PFMT in pregnancy, put the onus onto individual health care professionals and women to make decisions about teaching or doing the exercises without regard to all the factual information. Women ‘don't know what they don't know’. Are we truly accepting that one third of women will experience stress urinary incontinence by mid-age when this could potentially be prevented through ante-natal PFMT? We urge the panel to re-consider their recommendation and are happy to supply any further evidence as required to guide the evidence grading.
Kari Bø, Professor, PhD. The Norwegian School of Sport Sciences, Dept of Sports Medicine, Oslo, Norway.
Chantale Dumoulin, Professor, PhD. University of Montreal, School of Rehabilitation, Montreal, Canada
Cristine HJ Ferreira, Associate Professor, PhD, University of Sao Paulo, Ribeirao Preto Medical School, Ribeirao Preto, Brazil
Helena Frawley, Associate Professor, PhD, Monash University, Dept of Physiotherapy, Melbourne, Australia
Jean Hay-Smith, Associate Professor, PhD, University of Otago, Wellington, New Zealand
Siv Mørkved, Professor, PhD, Norwegian University of Science and Technology, Dept of Public Health and Nursing, Trondheim, Norway
Ingrid Nygaard, Professor, MD, MS, University of Utah, School of Medicine, Salt Lake City, USA
Margaret Sherburn, PhD, Physiotherapy, School of Health Sciences, The University of Melbourne, Melbourne, Australia
References
Bø K. Urinary Incontinence, Pelvic Floor Dysfunction, Exercise and Sport. Sports Med 2004; 34: 451-464.
Bø K,Hagen RH, Kvarstein B, Jørgensen J, Larsen S. Pelvic floor muscle exercise for the
treatment of female stress urinary incontinence: III.Effects of two different degrees of pelvic floor muscle exercises. Neurourol Urodyn; 1990: 9,5:489-502.
Davenport MH, Nagpal TS, Mottola MF et al. Prenatal exercise (including but not limited to pelvic floor muscle training) and urinary incontinence during and following pregnancy; a systematic review and meta-analysis. Br J Sports Med 2018; 52: 1397-1404.
Davenport MH (B), Ruchat SM, Sobierajski F et al. Impact of prenatal exercise on maternal harms, labour and delivery outcomes: a systematic review and meta-analysis. Br J Sports Med. 2018 Oct 18. pii: bjsports-2018-099821. doi: 10.1136/bjsports-2018-099821. [Epub ahead of print]
Fernandes da Mota PG, Pascoal AG, Carita AI, Bø K. Prevalence and risk factors of diastasis recti abdominis from late pregnancy to 6 months postpartum, and relationship with lumbo-pelvic pain. Man Ther 2015; 20:200-2005
Hamid TA, Pakgohar M, Ibrahim R, Dstjerdi MV. "Stain in life": The meaning of urinary incontinence in the context of Muslim postmenopausal women through hermeneutic phenomenology. Archieves Geront Geriatr 2015; 60: 514-521.
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Dear Dr. McGuine et al,
I'd like to commend you on running a large RCT on such an important topic (assessing the purported effectiveness of concussion-reduction technologies). Unfortunately I have some concerns about some aspects of your data and analysis, particularly the as-treated analysis in Table 4and your reported adherence numbers. I am hoping you can clarify these concerns and re-do parts of your analysis.
1. In the as-treated analysis you have a very strange result. Your multivariate risk ratio (which is actually a rate ratio) is 0.63 for everyone overall, 0.64 for females, and 0.93 for males. The result for everyone should be between the results for males and females. Can you please clarify how you got these results, including the exact model(s) you used and how you calculated the rate ratios? Did you use a group*sex interaction term to get the sex-specific results?
2. How you defined the as-treated group is concerning. You state that you only re-classified a subject if they spent >50% of their time in their non-assigned group OR if they were concussed while in their non-assigned group. This approach will bias the results of your as-treated analysis as you are deliberately misclassifying the AEs of people who do not get hurt and the non-concussed AEs of those who do. You need to classify every AE, rather than each athlete, as headgear or no headgear and repeat the as-treated analysis. Otherwise this analysis is highly questionable and...
Show MoreDear Dr. Anoop Balachandran
We would like to thank you for your insightful and interesting comment.
Regarding the first point, we presented the 28.5% to illustrate the relative difference in total absolute fat (kg) change between interventions, so the reader could have information about the relative difference between groups. We would like to highlight that it was only possible to perform this analysis using the within group changes, since the change between group analysis was showed in absolute values.
About the second point, it was not our purpose to analyse lean body mass; however, we agree that this topic is very important for health and athletic performance purposes. This is an unanswered question and we are performing studies to test the effects of interval training on lean body mass to help shedding light in the topic.
Best regards.
In this article the authors discuss their analysis of 21 female and 22 male athletic events. Testing all 43, they find 3 events significant with p<0.05. When testing 43 events, the expectation is that a well-calibrated statistical test will produce 2 false positives with random data, on average, due to the definition of the p-value. The odds of producing 3 false positives are also rather high; for normally distributed simulated data under the null, I found 3 or more false positives approximately 1/3 of the time such an analysis is performed, see here for a simulation notebook: https://github.com/davidasiegel/False-Positive-Rate-for-Multiple-Tests-i....
This is why adjustments for multiple comparisons needs to be performed. It was neglected in their initial study and neglected again in this study. In the 2017 study they state, "These different athletic events were considered as distinct independent analyses and adjustment for multiple comparisons was not required." This doesn't make sense to me; if the analyses are distinct, then all the more reason to correct for multiple comparisons. If a Bonferroni correction were performed, none of the p-values would test significant at the level of the study (p<0.05/43 = 0.001). Therefore I do not see why there is any reason to reject the null hypothesis for any of these results.
Perfor...
Show MoreFor readers who are following the debate about how training load may relate to injury, Dr Johann Windt considers the implication of the correlation that is pointed out here. Thanks to all the authors. k2
https://bjsm.bmj.com/content/early/2018/05/28/bjsports-2017-098925
The study raises two questions that one of the authors might be able to help with:
First, the authors report both within group and between group changes in body fat in the abstract. But it is unclear why the authors chose the within-group changes (28% fat loss) as the study conclusion than the between-group change.
The within group change showed a fat loss of 0.45 kg (28%) in favor of interval training (IT), while the between-group changes showed a large difference of 2.28 kg of fat loss in favor of IT. Considering the large difference in fat loss, and some studies recommending to avoid within group differences in meta-analysis, it would be helpful if the authors could comment on this.
Second, maintaining lean body mass (LBM) is one of the primary reasons to include exercise as part of a weight loss strategy. So it is not clear why the authors chose not to include lean body mass as one of the outcomes. It would have certainly helped the reader to make a decision regarding the choice of exercise for weight loss.
Finally, congratulations to all the authors for asking a very relevant question!.
We thank Freke et al. (1) for their systematic review about physical impairments in patients with symptomatic femoroacetabular impingement, nonetheless we have some remarks about methods and results of the article, in particular for range of motion (ROM) outcome.
Show MoreA meta-analysis of ROM was performed without reporting an overall estimate. Taking into account the amount of studies included and their information, a meta-analysis should have been accomplished. Nonetheless, authors concluded that individuals with symptomatic FAI demonstrated no difference in hip ROM in any direction of movement. This conclusion was unexpected taking into account the findings reported in the primary studies included), and in the previous systematic review published in 2015 (2), that showed instead a reduced ROM.
This discrepancy in literature is already discussed by the Warwick agreement (3), where authors stated that “the evidence on hip range of motion (ROM) in FAI syndrome is surprisingly contradictory” due to contrasting published systematic reviews (1) (2).
Therefore, we checked the accuracy of results reported, analyzing the data reported for every movement assessed in primary studies comparing those reported in this systematic review. We noted some issues in the represented forest plots.
Firstly, some included studies (4), (5), (6), (7) were reported twice in the meta-analysis for different times points or reporting double data of the same patients obtained by two...
Dear Editor,
I would like to congratulate the British Journal of Sports Medicine for the publication of the study ‘The Adductor Strengthening Programme prevents groin problems among male football players: a cluster-randomised controlled trial’ conducted by Harøy et al.[1]. The study investigated the effect of the adductor strengthening programme on the prevalence of groin problems among football players. The findings are incredibly important for the development of sports medicine because of their clinical relevance.
Regarding the methodology of this study, rather than giving criticism, I would like to suggest the authors if they can provide additional information or even a follow-up article on the game performance of the football teams involved in this study. As mentioned in the article, the authors have considered the groin pain causing time loss, decreasing participation or performance of the players [1]. Meanwhile, the previous study literally found that a lower incidence rate was strongly correlated with the number of goals, games won and even team ranking position [2,3]. Therefore, readers are interested whether the performance could be improved too since the results showed a significant reduction in the prevalence of groin pain in the players.
Similar studies have been conducted to investigate the effect of a specific strength training programme on players’ injury prevalence and individuals’ performance [4]. However, no data was included to refl...
Show MoreMany of you will be familiar with The BMJ and its popular 'Rapid Responses'. Because we are a sister journal to The BMJ (and part of the same publishing company of course) we have the same Platform and we encourage you to use it.
Why is this in BJSM? In general, it is best to have papers go through peer review in the most relevant journal to their subject matter to ensure that the production team is well placed to find suitable editors and reviewers.
Letter to the Editors
Show MoreBr J Sports Med
J Obstet Gynecol Canada
Oslo, Nov 23rd 2018
Comment and questions to Mottola et al (2019): 2019 Canadian guideline for physical activity throughout pregnancy
We have read the Canadian guideline for physical activity throughout pregnancy with great interest. We note that the guideline team have made their recommendation regarding pelvic floor muscle training (PFMT) based on evidence from a systematic review from the same research group (Davenport et al 2018). The main results of this review are in line with the latest Cochrane review (Woodley et al 2017) on the same topic; while there are some methodological differences and variations in which studies were included or not (two of the largest studies on PFMT was left out from the Davenport review; Mørkved et al 2003 and Stafne et al 2012), the findings in terms of size and precision of effect are similar, although Davenport et al used odds ratio and Woodley et al used risk ratio for their summary statistic. Davenport et al reported that PFMT gave a 50% reduction in prenatal UI and a 35% reduction in postnatal UI, but the guideline team concluded a “weak recommendation” for PFMT because UI was not rated as a "critical outcome" and the evidence was of "low quality". We find this conclusion at odds with the evidence and the interpretation of the evidence based on the guideline team’s own criteria.
The Canadian guideline grades...
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