Shiri et al. conducted a meta-analysis to examine the effect of leisure time physical activity on non-specific low back pain (LBP) (1). Adjusted risk ratio (RR) (95% confidence interval) of moderately/highly active individuals, moderately active individuals and highly active individuals against individuals without regular physical activity for frequent/chronic LBP was 0.89 (0.82 to 0.97), 0.86 (0.79 to 0.94) and 0.84 (0.75 to 0.93), respectively. For LBP in the past 1-12 months, adjusted RR did not reach the level of significance in any levels of physical activity. The authors concluded that leisure time physical activity might reduce the risk of chronic LBP by 11%-16%. I have some concerns about their study by presenting negative information regarding protection of LBP by physical activity.

First, Saragiotto et al. conducted a meta-analysis on the effectiveness of motor control exercise (MCE) in patients with nonspecific LBP (2). MCE focuses on the activation of the deep trunk muscles and targets the restoration of control and coordination of these muscles. They concluded that MCE was probably more effective than a minimal intervention for reducing pain, but did not have an important effect on disability, in patients with chronic LBP. In addition, there was no clear difference between MCE and other forms of exercises or manual therapy for acute and chronic LBP. Although there is no definite information to recommend MCE for non-specific LBP, further studies are needed to verify the interventional effects.

Second, Øverås et al. reviewed prospective studies to evaluate the associations between objectively measured physical behaviour and the risk or prognosis of neck pain (NP) and/or LBP (3). Eight studies out of 10 handled blue-collar workers, and increased sitting time at work reduced the risk of NP and LBP. Among blue-collar workers, increased physical activity during work and/or leisure increased the risk of NP and LBP. In addition, physical activity was not significantly associated with prognosis of LBP. These findings are not consistent with data by Shiri et al. (1), and type of job might be an important factor on the association.

Finally, Oliveira et al. reviewed prospective studies to investigate the prognostic role of physical activity in the course of LBP (4). Although low quality evidence presented that physical activity might not be a prognostic factor for pain and disability in patients with LBP, additional studies are indispensable to verify the association. I speculate that many factors would affect the relationship and might be complicated.

References

1. Shiri R, Falah-Hassani K. Does leisure time physical activity protect against low back pain? Systematic review and meta-analysis of 36 prospective cohort studies. Br J Sports Med. 2017;51(19):1410-1418. doi: 10.1136/bjsports-2016-097352

2. Saragiotto BT, Maher CG, Yamato TP, et al. Motor control exercise for nonspecific low back pain: A Cochrane review. Spine (Phila Pa 1976). 2016;41(16):1284-95. doi: 10.1097/BRS.0000000000001645

3. Øverås CK, Villumsen M, Axén I, et al. Association between objectively measured physical behaviour and neck- and/or low back pain: A systematic review. Eur J Pain. 2020 Feb 24. doi: 10.1002/ejp.1551

4. Oliveira CB, Pinheiro MB, Teixeira RJ, et al. Physical activity as a prognostic factor of pain intensity and disability in patients with low back pain: A systematic review. Eur J Pain. 2019;23(7):1251-1263. doi: 10.1002/ejp.1395

We read with interest, and concern, the letter submitted by Schilaty et al arguing bias in our analysis examining the association between concussion and mouthguard use. Schilaty et al argue that a nested case-control study was not optimal and that “Based on a relatively small cohort, a complete case-control study would have been more appropriate than a nested case-control study.” They then go on to argue that “selection criteria of the non-concussion group biased the study as a random sample was not selected from the remaining cohort (n=2,040)” eliminating “from the analysis all non-injured players who wore mouthguards.” Finally, Schilaty et al contend that our study did not “properly compare the incidence of concussion between wearers or non-wearers of mouthguards.” There are multiple concerning statements and assertions made by the authors of the letter, Schilaty et al., that we will address below.

Shilaty et al discuss the desire to compare “incidence of concussion between wearers and non-wearers of mouthguards.” Incidence cannot truly be estimated from a case-control study, given that the number of cases and controls is fixed from the design. Rather, we are after the odds ratio based on the ratio of the odds of exposure in cases relative to controls (the odds ratio of exposure is mathematically the same as the odds ratio of being a case). Modern conceptualizations of the case-control study invoke the idea of pseudo frequencies or quasi-rates related to construction of the odds ratio and what it means.[1,2,3] Regardless, the control group in a case-control study is intended to reflect the exposure (e.g., mouthguard) use in the source population that produced the cases (e.g., concussions).[1] We feel strongly that our control group of non-head injuries reflects well the mouthguard use experience in this source population and that it was sampled independently of exposure status.

Schilaty et al argue that non-random selection of controls resulted in bias because it “eliminated from the analysis all non-injured players who wore mouthguards.” We agree that if all non-concussed players were wearing mouthguards, then this would have biased our results. However, Schilaty et al don’t seem to appreciate that some of those non-injured players who would have been selected in a random sample would have been using mouthguards and importantly, some would not. There is nothing inherently biased in sampling non-concussion, but still injured controls who may more accurately capture the mouthguard experience of the source population that produced the cases. It is this split of the proportion in the mouthguard exposed and unexposed groups we are after to tell us what the expectation should be for the cases, under the null hypothesis of no effect of mouthguards. That is, “we want the control group to provide estimates of the relative size of the denominators of the incidence proportions or incidence rates for the compared groups.”[1] Also, it is what allows us to calculate the odds ratio as the measure of effect in a case-control study. Ironically, if the bias Schilaty et al propose did in fact exist (i.e., that all or even a larger percentage of non-selected non-injured controls were using mouthguards), it would have resulted in an even more protective mouthguard effect than what we found-no additional analysis required!

It is very interesting that Schilaty et al are asking us "to estimate mouthguard compliance among youth players and use the estimated trends for all control subjects”. We discussed in the paper that our investigation was conducted within cohorts assembled for other reasons. As such, we had no opportunity to sample controls in a random fashion as Schilaty et al proposed. The very reason we wanted to use the methodologically rigorous approach we chose was to avoid making assumptions about mouthguard use for the entire cohort (given that mouthguard use was the main exposure) and address the potentially important issue of confounding by other factors (e.g., mechanism of injury). The analysis the authors of the letter are arguing for would likely result in an effect more biased toward the null (no effect). This would not be because of a superior sampling approach, but because of misclassification bias of mouthguard use among controls. A serious issue to be sure, and one that Schilaty et al even acknowledge as adding “an additional limitation to the study.”

We are concerned that Schilaty et al are mixing up the issue of random error and systematic error. More subjects in what they describe as a “complete case-control study” would potentially reduce random (i.e., statistical) error, but in isolation, would have no effect on the systematic error of the estimates. That is, a larger sample may provide a more precise estimate (narrower confidence limits), but it does not guarantee less bias.

Regarding the issue of causality, we agree more work is required to understand the primary mechanisms of concussion and how mouthguards may reduce the risk. However, this was not the focus of our study and we were simply outlining potential explanations. We do agree that there continue to be gaps in the evidence base that need to be addressed from a causal mechanism perspective.

In summary, we clearly outlined our methodological and conceptual rationale for the rigorous case-control approach we used in our paper and acknowledged limitations. Our approach was feasible and produced what we argue is strong evidence on the mouthguard-concussion relationship. Schilaty’s approach would involve artificially estimating mouthguard use for thousands of children and sampling from that distribution at, presumably, the time of a concussion. This would add significant limitations to the analysis in terms of capturing mouthguard use and key covariates essential for addressing potential confounding. We respectfully disagree with the approach suggested by Schilaty et al and feel it would be much less methodologically and analytically defensible than what we outlined in our paper.

REFERENCES
1. Rothman, Greenland, Lash. Chapter 8: Case-control studies. Modern Epidemiology. Third Edition. Lippincott Williams & Wilkins, 2008.

2. Miettinen OS. Etiologic research: Needed revisions of concepts and principles. Scand J Work Environ Health 1999; 25 (6, special issue):484-490.

3. Miettinen OS. Epidemiological research: Terms and concepts. Springer, 2011.

We read with interest the recent International Olympic Committee consensus statement: methods for recording and reporting of epidemiological data on injury and illness in sport 2020 (including STROBE Extension for Sport Injury and Illness Surveillance (STROBE-SIIS))”.[1] While helping to clarify aspects associated with recording and reporting epidemiological data, based on the definitions included in the statement, we believe that some of the examples in Table 10 require clarification with regards to the recording of injuries and calculation of time loss.

Consider the example for ‘Delayed’ time loss: Sunday injury, thigh contusion, able to train on Monday and Tuesday but unable to train on Wednesday and returns on Sunday (time loss starts on Wednesday even though the injury was on Sunday). Time loss (days) 3. Given the recommended reported time loss of 3-days, and definition provided whereby “time-loss days should be counted from the day after the onset that the athlete is unable to participate”, we assume Wednesday is considered as the day of onset (day 0), with subsequent impact on Thursday, Friday and Saturday resulting in a 3-day time-loss (days). When considering this example, we were then somewhat confused by the example for, ‘Intermittent’ time loss: boy with Osgood-Schlatter disease that gets reported at the start of a training camp on Monday. The player may train fully on Monday, Tuesday and Thursday, but miss training on Wednesday and Friday (time loss counted as Wednesday and Friday only). Time loss (days) 2. Herein, applying the time-loss definition provided in the consensus statement [1] and the logic applied to the delayed time loss example, should the Wednesday not be considered as the onset of time loss and therefore counted as day 0? Based on the two examples and the time-loss (days) provided for each we feel as if time-loss (days) has been calculated differently and as such wish for the authors to clarify. From our position we agree with recording time-loss from the day after the injury when the injury occurs during training on that day, but if an athlete is unable to participate at all due to injury we feel as if this could be considered day 1 of time-loss.

In relation to the above examples it is also unclear as to why these have been considered as single injury reports (cases) given the definitions provided within the consensus statement, “subsequent injuries to the same location and tissue as the index injury are recurrences if the index injury was healed/fully recovered; they are exacerbations if the index injury was not yet healed/fully recovered”, when healed/fully recovered is when an “athlete is fully available for training and competition”.[1] Herein, for the delayed time loss and intermittent time loss examples we would interpret that the injury examples should be considered as multiple injury reports (cases). For delayed time loss, the first case would open following the initial injury on the Sunday and close when the athlete is considered healed/fully recovered, when they return to full training Monday, before a subsequent recurrence on the Wednesday, second case open, which closes on the Sunday (Figure 1a). Similarly for intermittent time loss, it seems that the initial case opens with the initial injury report Monday, closes when the athlete trained fully Monday, second injury case opens on Wednesday as the athlete is unable to train and closes Thursday upon full return to training, before another case opens on the Friday (Figure 1b).

INSERT FIGURE 1A AND 1B ABOUT HERE

Moreover, if the intermittent time loss example should in fact be considered as multiple injury reports (cases), based on time-loss methods suggested within the paper, both Wednesday and Friday would be considered as the onset of time loss and counted as day 0. Therefore, although the athlete missed two days of training, 0 time loss (days) would be calculated (Figure 1b). As a result such an approach for calculating time loss may lead to underreporting. We feel as if this supports our view that an athlete reporting injured at the start of training (and does not participate at all), incurs the first day of time loss and in this example results in two 1-day time-loss events linked to two subsequent injury reports (cases).

It is not our intention to challenge the authors and indeed the updated consensus statements has provided valuable recommendations for injury surveillance. Additionally, we are pleased to see the inclusion of examples within the paper as in our areas of research such examples are a regular occurrence. However, based on the two examples provided, we feel that there are discrepancies with regards to the calculation of time-loss (days) and a lack of clarity surrounding injury recording, specifically with respect to what keeps an injury report (case) open (delayed and intermittent time loss examples). We therefore ask the authors to consider clarification on each point we raise in this letter.

References
Bahr R, Clarsen B, Derman W, et al. International Olympic Committee consensus statement: methods for recording and reporting of epidemiological data on injury and illness in sport 2020 (including STROBE Extension for Sport Injury and Illness Surveillance (STROBE-SIIS)). Br J Sports Med Published Online First: 18 February 2020. doi: 10.1136/bjsports-2019-101969

Figure Descriptions
Figure 1: Injury examples from the International Olympic Committee consensus statement, with the inclusion of injury cases and associated time loss (days), based on the healed/fully recovered and time loss (days) definitions provided.

Tables and Figures
Figure available upon reasonable request

In the mid-1990s, as one of the reviewers for the American Heart Association, the first author of this letter, Dr Richard M Fleming (RMF) introduced a then controversial theory stating that Coronary Artery Disease (CAD) is the result of an inflammatory process, which builds up within the walls of the arteries (Figure 1) impairing their ability to dilate and increase coronary blood flow when needed; thus producing regional blood flow differences resulting in angina [1-3] and ultimately myocardial infarction (MI) and death.
In recent years, people promoting various dietary and lifestyle practices – particularly those promoting LowCarb-Keto diets, have taken advantage of the obesity epidemic and focused everyone’s attention on obesity and weight loss. These individuals have not determined the actual impact their diets have on CAD - which would require more than just looking at changes in weight or serum blood tests. It would require measurement of changes occurring within the walls of the coronary arteries themselves – not some other artery - and the resulting change in coronary artery function [1,4].
These individuals, including Dr. Aseem Malhotra [5] support their dietary recommendations by showing weight loss, and occasionally reductions in cholesterol levels – at least initially in some people. Over the years as it has been shown that cholesterol levels fail to fall, and frequently increase on such diets, their argument has changed and has been replaced with “saturated fat does not clog the (coronary or other) arteries” [5].
We argue that the claim by Malhotra, and others -- that saturated fat and LDL-cholesterol have nothing to do with the development of inflammatory CAD – demonstrates a complete failure to understand the “Inflammation and Heart Disease” Theory [3,6] as shown in Figure 1 and therefore cannot be taken seriously.
Their claims introduce yet another major misconception into the discussion of CAD. Specifically, the process of “clogging of the coronary arteries.” The narrowing or “clogging” of the coronary artery lumen – where the blood flows - so frequently referred to as CAD, is actually a late process in the development of the inflammatory changes that are CAD [7-13].
CAD begins with the inflammatory process first distending the wall of the artery outward away from the lumen – impairing the function of the artery - and only later encroaching upon the lumen itself [1,3,7]. Recognition that the rupture of this inflammatory process may occur following minimal or no coronary lumen narrowing [1,3,7] has resulted in the recent acknowledgement by the Cardiology community that infarction of myocardium may occur with (Type I) or without (TYPE II) coronary lumen obstruction.
Fleming and Harrington’s work – published in 2008 [14] - demonstrated that the relationship between weight loss, and changes in lipids and other blood tests reflecting inflammatory processes [3], are only mildly-to-moderately correlated (Figure 2) with actual changes occurring within the coronary arteries themselves. Thus further exposing the erroneous statement - using the results of blood tests - declaring that saturated fat and cholesterol are not involved in CAD.
To understand the impact LowCarb-Keto diets - or for that matter any diet - has on CAD, one needs to measure what is happening to the coronary arteries themselves [15-17] by using FMTVDM.
To state that Saturated fat and LDL-cholesterol has nothing to do with CAD and do not result in the “clogging” of coronary arteries, and then to state that CAD is a chronic inflammatory condition - raises serious concerns about the motivation of their arguments. It also raises serious questions about their actual understanding of the ”Inflammation and Heart Disease” Theory. To which we acknowledge, “we can teach it to you but we cannot understand it for you.”

Acknowledged potential COI: FMTVDM (The Fleming Method for Tissue and Vascular Differentiation and Metabolism) [4] is issued to the first author. The first author authored the Inflammation and Heart Disease and Angina Theories.

RM Fleming and Matthew R Fleming, FHHI-OI-Camelot
TK Chaudhuri, Eastern Virginia Medical School.

Figures available upon reasonable request:
Figure 1. Fleming Inflammation and Heart Disease Theory first introduced in the 1990s [3].
Figure 2. Changes in weight loss and serum markers of lipids and other inflammatory blood tests correlate only mildly-to-moderately with actual measured changes in coronary artery disease [14].

References:
1. Fleming RM. Chapter 29. Atherosclerosis: Understanding the relationship between coronary artery disease and stenosis flow reserve. Textbook of Angiology. John C. Chang Editor, Springer-Verlag, New York, NY. 1999. pp. 381-387.
2. Fleming RM. Chapter 30. Cholesterol, Triglycerides and the treatment of hyperlipidemias. Textbook of Angiology. John C. Chang Editor, Springer-Verlag, New York, NY. 1999, pp. 388-396.
3. Fleming RM. Chapter 64. The Pathogenesis of Vascular Disease. Textbook of Angiology. John C. Chang Editor, Springer-Verlag New York, NY. 1999, pp. 787-798.
4. The Fleming Method for Tissue and Vascular Differentiation and Metabolism (FMTVDM) using same state single or sequential quantification comparisons. Patent Number 9566037. Issued 02/14/2017.
5. Malhotra A, Redberg R, Meier P. Saturated fat does not clog the arteries: coronary heart disease is a chronic inflammatory condition, the risk of which can be effectively reduced from healthy lifestyle interventions. British J Sports Med 2017;51:1111-1112.
6. 20/20 Segment on Heart Disease and Inflammation. https://www.youtube.com/watch?v=Hvb_Ced7KyA&t=22s
7. Glagov S, Weisenberg E, Zarins CK, Stankunavicius R, Kolettis GJ. Compensatory enlargement of human atherosclerotic coronary arteries. N Engl J Med 1987;316(22):1371-1375.
8. Fleming RM., Kirkeeide RL, Smalling RW, Gould KL. Patterns in Visual Interpretation of Coronary Arteriograms as Detected by Quantitative Coronary Arteriography. J Am Coll. Cardiol. 1991;18:945- 951.
9. Fleming RM, Harrington GM. Quantitative Coronary Arteriography and its Assessment of Atherosclerosis. Part 1. Examining the Independent Variables. Angiology 1994;45(10):829-833.
10. Fleming RM, Harrington GM. Quantitative Coronary Arteriography and its Assessment of Atherosclerosis. Part 2. Calculating Stenosis Flow Reserve Directly from Percent Diameter Stenosis. Angiology 1994;45(10):835-840.
11. Fleming RM. Shortcomings of coronary angiography. Letter to the Editor. Cleve Clin J Med 2000;67:450.
12. Fleming RM. Coronary Artery Disease is More than Just Coronary Lumen Disease. Amer J Card 2001;88:599-600.
13. Fleming RM, Harrington GM. TAM-A.7 Sestamibi redistribution measurement defines ischemic coronary artery lumen disease. 56th Annual Meeting of the Health Physics Society. (American Conference of Radiological Safety) West Palm Beach, FL, USA, 30 June 2011. http://hpschapters.org/2011AM/program/singlesession.php3?sessid=TAM-A
14. Fleming RM, Harrington GM. What is the Relationship between Myocardial Perfusion Imaging and Coronary Artery Disease Risk Factors and Markers of Inflammation? Angiology 2008;59:16-25.

15. Fleming RM, Fleming MR, Chaudhuri TK. Replacing Cardiovascular Risk Factors with True AI and Absolute Quantifiable Measurement (FMTVDM) of Coronary Artery Disease. Inter J Res Studies Med & Health Sci. 2019;4(11):11- 13. ISSN:2456-6373.
16. Fleming RM, Fleming MR, Chaudhuri TK. Are we prescribing the right diets and drugs for CAD, T2D, Cancer and Obesity? Int J Nuclear Med Radioactive Subs 2019;2(2):000115.
17. Fleming RM, Fleming MR, Chaudhuri TK, Harrington GM. Cardiovascular Outcomes of Diet Counseling. Edel J Biomed Res Rev. 2019;1(1):20-29.