Displaying 1-10 letters out of 521 published
Please don't forget the role of Vitamin K2 in CAD
I read the elaborate study design of this interesting and expensive study. The authors deserve congratulations for addressing the common issue amongst elderly people.
The data is emerging about high intake of Vitamin K2 (menaquinone)linking with reduced coronary calcification.1
In Rotterdam study dietary intake of Vitamin K2 is associated with reduced risk of coronary artery diseaes (CAD).2 It is timely, the vitamin K2 is also included in the assessment in this elaborate study.
Many elderly patients opt for non-invasive management of CAD, therefore such patients should not be excluded from the study design, particularly while focusing on real life design of the study.
1.Beulens JW1, Bots ML, Atsma F, et al. High dietary menaquinone intake is associated with reduced coronary calcification.Atherosclerosis. 2009 Apr;203(2):489-93.
2. Geleijnse JM, Veermeer C, Diederick EG, et al. Dietary Intake of Menaquinone Is Associated with a Reduced Risk of Coronary Heart Disease:The Rotterdam Study. J.Nutr. November 1, 2004 vol. 134 no. 11 3100 -3105
Conflict of Interest:
Faulty reporting about mortality regarding women, the elder, and others.
The Johns Hopkins authors, Eatz et al, critique Ravnskov et al for poor science and methods and then they state this: " Given that statins are known to reduce all-cause mortality .." This ignores the fact that there has NEVER been a placebo controlled cholesterol-lowering intervention that ended with a mortality benefit in women, and this includes statins.
For example, the land mark 4S study ended with 3 more women heart- patient deaths on statin, while 2 other large supposedly "successful" trials [HPS and ASCOT] have refused to report on women's deaths, a dozen years after completion -but we know at least for HPS that it was not significant.
SPARCL in (mainly) ischemic stroke patients ended with numerically more death on the statin.
Moreover, the one study in over 70 year olds, the placebo controlled PROSPER study [part primary / part secondary prevention], ended without a mortality benefit but with a p-value for increased "newly diagnosed cancer" [the frightening serious type] of p=0.02. Who would not prefer the placebo?
There are now 4 large rosuvastatin [Crestor] vs placebo studies, 2 ending without a cardiovascular mortality benefit [both p=~0.35; JUPITER, HOPE-3] and 2 without benefit in any vascular department [CORONA, AURORA] .
For any of those patients, the quote in the first paragraph is wrong, misleading and potentially harmful.
Conflict of Interest:
Re:Effectiveness of the Assessment of Burden of COPD (ABC) tool on health-related quality of life in patients with COPD: Twitter Discussions from the University of Toronto Respirology and Sleep Journal Club (@respandsleepjc)
In their correspondence on our cluster randomised controlled trial evaluating the Assessment of Burden of COPD (ABC) tool, Abhyankar and colleagues raise some issues regarding the reported results and its implications. First, we would like to clarify that the PACIC is not a questionnaire measuring quality of life, but quality of care as experienced by patients. With respect to randomisation, sample size and baseline imbalance, the discussants express concerns that are understandable but unfounded, as we will now explain. Page 3 of our paper clearly states the randomisation procedure used, but of course chance imbalance in spite of randomisation can occur (we get back to this point below). Page 4 and reference 17 give all details of the sample size calculation, showing this study to be sufficiently powered. In fact, with a total of about 60 clusters, this trial is certainly not small. For instance, a review by Adams and colleagues of 19 cluster randomised trials found a median number of clusters of 41, with an interquartile range of 24 to 64.1 Our answer to the worry about baseline imbalance and regression to the mean is necessarily a bit longer and more technical, so please bear with us. We focus on the total SGRQ score, but the reasoning applies equally to the other outcome measures reported.
For the total SGRQ score, the group difference at baseline as evaluated by our mixed regression model (for details, see page 4) had a p- value of 0.195, far from significant. Moreover, the reported effect analyses do adjust for any baseline imbalance as well as for regression to the mean. The initial mixed regression model included treatment arm as predictor on top of time and treatment by time effects, thus allowing for a group difference at baseline (since baseline was the reference category for time). The treatment by time interaction effect in that model is equivalent to the difference between treatment arms with respect to change from baseline (for a proof and demo, see Van Breukelen2,3). Now, as stated on page 4 bottom - page 5 top, if the group difference at baseline was not significant then it was removed from the model. The treatment by time effect of interest then became equivalent to the treatment effect at follow-up adjusted for the baseline as a covariate.4 This equivalence cannot be seen intuitively, but formal proofs and empirical demonstrations are given in Liu et al.5 and Van Breukelen.2,3 Since the baseline group difference on SGRQ total was far from significant, it was removed from the model, and Table 2 in our paper reports the treatment group differences at each follow-up based on the reduced mixed model (which comes down to adjusting for baseline as a covariate). The effect size and significance before model reduction was very similar to the one reported after reduction (beta = 3.36 instead of 3.08, and p = 0.005 instead of 0.008 at 18 months follow-up). Both the model reduction and the similarity between effects before and after reduction are stated in a footnote to Table 2. Relatedly, the chance imbalance in FEV1 and FEV1/FVC ratio that the discussants worry about, was adjusted for by including both measures as covariates in a secondary analysis, and this gave results very similar to those of the primary analysis (see page 6 bottom - page 7 top). '
To appreciate these results, please note that in an RCT both methods of analysis, change from baseline (our mixed model with baseline group effect) and adjustment for baseline as a covariate (mixed model without baseline group effect), are unbiased. This means that, in the long run of an infinite number of replications, both methods give the true treatment effect on the average. Further, the covariate adjustment method is even unbiased given baseline imbalance in a single RCT.6-8 This is because the covariate adjustment method takes regression to the mean into account. In our case, this regression to the mean effect was very small because the correlation between SGRQ at baseline and at 18 months follow-up was as high as 0.80. This also explains why the two methods of analysis, change from baseline (mixed model with baseline group difference) and covariate adjustment (mixed model without baseline difference) gave quite similar effects at follow-up. This answer and our paper would have been more simple if we had analysed our data with the classical methods. One of the reasons for using mixed models was to include all randomised clusters and patients in spite of dropout (intention-to-treat analysis), which is possible with mixed regression but not with the classical methods. As Figure 2 in our paper shows, there was sufficient dropout to justify our approach. In fact, there was some very small dropout even before baseline, which can hardly be prevented in a cluster randomised trial because clusters are randomised at the start of the trial, whereas patients are measured as they come in. It was because of this small dropout before baseline that we applied and compared both methods, the mixed model with and without baseline group difference. As said before, we did not find a significant baseline difference and we reported the treatment effects at follow-up based on the reduced mixed model.
There is much more to be said about regression to the mean and about the best method of analysis than can be done in this reply, see e.g. Senn8 and Van Breukelen2,3. The point here is that (a) there is no convincing evidence of a true baseline imbalance in our trial, and (b) the methods of analysis used take any imbalance into account in the best possible way, and (c) the treatment effect reported is not an artefact of regression to the mean.
1. Adams G, Gulliford MC, Ukoumunne OC, Eldridge S, Chinn S, Campbell MJ (2004). Patterns of intracluster correlation from primary care research to inform study design and analysis. Journal of Clinical Epidemiology , 57 , 785-794. 2. Van Breukelen GJP (2006). ANCOVA versus change from baseline: more power in randomized studies, more bias in nonrandomized studies. Journal of Clinical Epidemiology, 59, 920-925. 3. Van Breukelen GJP (2013). ANCOVA versus change from baseline in nonrandomized studies: the difference. Multivariate Behavioral Research, 48 (6), 1-28. 4. Laird NM, Wang F (1990). Estimating rates of change in randomized clinical trials. Controlled Clinical Trials, 11, 405-419. 5. Liu GF, Lu K, Mogg R, Mallick M, Mehrotra DV (2009). Should baseline be a covariate or dependent variable in analyses of change from baseline in clinical trials ? Statistics in Medicine, 28, 2509-2530. 6. Senn SJ (1989). Covariate imbalance and random allocation in clinical trials. Statistics in Medicine, 8, 467-475. 7. Senn SJ (1994a). Testing for baseline balance in clinical trials. Statistics in Medicine, 13, 1715-1726. 8. Senn SJ (1994b). Repeated measures in clinical trials: analysis using mean summary statistics and its implications for design (Letter to the editor). Statistics in Medicine, 13, 197-198.
Conflict of Interest:
Request for correction
We would like to make corrections on the above paper. We assure you the corrections are minor, and do not affect the analyses and the conclusions we made in the paper.
1) Page 2, 3rd line in the last paragraph
(current) "quintiles of dietary Na-K ratio (mmol/mmol)." (correct) "quintiles of dietary Na-K ratio (mg/mg)."
2) Table 1. We have noticed that the unit for sodium-to-potassium ratio we provided was wrong. It should be "mg/mg," not "mol/mol", and this applies to "Men", "Women" and "Men and Women combined" in Table 1.
We would like to provide values in "mmol/mmol" unit as well corresponding to each value (mg/mg) in Table 1 as follows.
Sodium-to-potassium ration in mmol/mmol, mean (SD) for Q1, Q2, Q3, Q4, Q5 in Men were 2.20 (0.30), 2.78 (0.13), 3.22 (0.13), 3.71 (0.16), 4.75 (0.82); the corresponding range (min) (max) for men were (0.94) (2.57), (2.56) (3.00), (3.00) (3.45), (3.45) (4.02), (4.01) (10.36).
Sodium-to-potassium ration in mmol/mmol, mean (SD) for Q1, Q2, Q3, Q4, Q5 in Women were 2.07 (0.26), 2.63 (0.12), 3.05 (0.12), 3.52 (0.15), 4.47 (0.74); the corresponding range (min) (max) for women were (1.00) (2.41), (2.41) (2.83), (2.83) (3.26), (3.26) (3.81), (3.81) (9.84).
Sodium-to-potassium ration in mmol/mmol, mean (SD) for Q1, Q2, Q3, Q4, Q5 in Men and Women combined were 2.13 (0.29), 2.70 (0.15), 3.13 (0.15), 3.61 (0.18), 4.60 (0.79); the corresponding range (min) (max) for men were (0.94) (2.57), (2.41) (3.00), (2.83) (3.45), (3.26) (4.02), (3.80) (10.36).
Again, this change (i.e. correction) does not influence our results and conclusions because the quintiles of the participants remain the same regardless of the unit used. For further conversation on this issue, please email to Akira Fujiyoshi (email@example.com).
Thank you in advance for your understanding.
August 13, 2016 Akira Fujiyoshi (an author), MD, PhD. Akira Okayama (corresponding author), MD, PhD
Conflict of Interest:
Scientific flaws in the response by Eatz et al.
Tiffany Eats et al. claim that atherosclerosis is caused by many other factors than high cholesterol, and we agree. What we claim is that high cholesterol has no influence at all, because, as we have mentioned in our paper, many studies have shown that people with low cholesterol become just as atherosclerotic as people with high cholesterol. Eats et al. therefore demand that global risk assessment must account for other risk factors, but all studies included in our analysis have also performed multivariate corrections for other factors.
According to Eats et al. the reason why high LDL-C is not a risk factor for elderly is that many of those with high levels have died before the age of 60. This is not so. In Sweden for instance, 95 % of those who die from a cardiovascular disease have passed the age of 60, and even if it was right, why should we lower cholesterol in elderly people?
Eats et al. also claim that low LDL-C may be caused by cancer, which may explain their shorter life, but here they are wrong again. As we have explained in detail in our paper it is a well-established fact that it is just the opposite; low cholesterol predisposes to cancer.
They also claim that other frailties cause low LDL-cholesterol, but they have evidently not noticed that in studies including more than 75 % of the participants, such patients were excluded.
That some of the participants may have been on statin treatment and thus may have introduced a bias is of course true. However, no association between LDL-C and mortality was seen in the studies performed before the introduction of the statin drugs. Furthermore, in the largest study, the authors had calculated the risk in statin-treated and non-treated individuals separately. The risk among the statin-treated was lower than among those with the lowest LDL-C values, but it was significantly higher than among those with the highest LDL-C values.
Another objection from Eats et al. is that Bathum et al. did not inform about which risk factors they had corrected for providing insufficient evidence to conclude whether such corrections were made or not. But these authors did estimate survival by the Kaplan-Meier method and analysed it using the Cox proportional hazards model. As adjustments are made only for factors that are significantly different between the groups, this is evidently not a bias.
Eats et al. also claim that high LDL-C is a risk factor for mortality up to the age of 90, because by using Mendelian randomization it has been shown that mortality is associated with a high LDL genetic risk score. This is a common argument among those who support the cholesterol hypothesis, but association is not the same as causation. Other, undiscovered genes in the same individual may have opposite effects (1).
Eats et al. claim that the official guidelines are based on high quality, randomized controlled trial data. However, most of these trials included mostly younger individuals. It is also questionable to classify the statin trials as being of high quality, because as some of us have shown (2), the authors of these trials have used several deceptive methods to exaggerate the benefit and minimize the side effects.
We can understand that it is difficult to admit that an idea most researchers have believed in and propagated for during their whole career is wrong. We think however, that those who are able to do that will gain respect.
1. Glymour MM, Tchetgen EJ, Robins JM. Credible mendelian randomization studies: approaches for evaluating the instrumental variable assumptions. Am J Epidemiol, 2012;175:332-9.
2. Diamond DM, Ravnskov U. How statistical deception created the appearance that statins are safe and effective in primary and secondary prevention of cardiovascular disease. Expert Rev Clin Pharmacol, 2015;8:201 -10.
Conflict of Interest:
I have published books with criticism of the cholesterol campaign
Letter Regarding Critical Flaws in "Lack of an association or an inverse association between low-density-lipoprotein cholesterol and mortality in the elderly: a systematic review"
We write to express our deep concerns about the inappropriate conclusions expressed in the article "Lack of an association or an inverse association between low-density-lipoprotein cholesterol and mortality in the elderly: a systematic review"(1). We contend that the article has serious flaws that make its conclusions detrimental to public health and understanding. The article's counterintuitive findings on low-density- lipoprotein cholesterol (LDL-C) have been widely covered by the lay press. We as clinicians have received troubling inquiries from our patients as a result. The article superficially appears to be an intriguing study, but its flawed methodology yields results that skew reality and mislead the general public. Overall, it suffers from oversimplification, misplaced emphasis, and misinterpretation.
Specifically, the premise of the study is erroneous. The article states that since atherosclerosis and cardiovascular disease are mainly diseases of the elderly, the cholesterol hypothesis predicts that the association between cardiovascular mortality and total cholesterol should be at least as strong in the elderly as in young people(1). In fact, this is not what the cholesterol hypothesis predicts. To understand why requires a basic understanding of the process of atherosclerosis. Cardiovascular risk in an elderly person arises from the development of atherosclerosis over the preceding decades of life due to cumulative exposure to not only elevated cholesterol levels, but to other risk factors as well. In this regard, total cholesterol (and LDL-cholesterol) measured at a single point in time later in life is insufficient. Moreover, because atherosclerosis is multifactorial, global risk assessment must account for other risk factors, including hypertension, diabetes, and smoking(2,3).
The article confuses LDL-C as a biologically essential mediator of atherosclerosis with the fact that LDL-C, as a single risk factor, is a relatively modest biomarker of absolute risk(4). The article does not acknowledge that at any LDL-C level, if a patient has more risk factors of atherosclerosis, then they will face an increased risk of an event or dying. For example, a person with a lower LDL-C and serious comorbidity will have a risk that exceeds an otherwise healthy person with a higher LDL-C(5). Statin therapy lowers LDL-C and reduces adverse outcomes in both situations, but it is the absolute risk of the individual based on comprehensive risk assessment that determines the absolute risk reduction by effective therapies such as LDL-C lowering statins(2,3). Presence of clinical atherosclerotic cardiovascular disease or lifelong exposure to very high levels of LDL-C do not require global risk assessment, as absolute risk is so high that statin treatment provides substantial benefit.
In addition to misrepresenting the origins of atherosclerosis and cardiovascular risk, the article does not acknowledge well-established epidemiological biases that threaten the validity of the reported findings. These biases include survivor and selection bias. Many people who suffered from high cholesterol and heart disease will have died off before age 60, falling below the threshold of this study. In other words, a substantial amount of people who would exhibit a strong correlation between hyperlipidemia and mortality are not accounted for. In fact, persons with high LDL-C who survive into their 60s and beyond will tend to have other favorable aspects to their global risk profile.
In contrast, some participants may have low LDL-C levels due to unfavorable underlying causes, such as occult cancer. The article suggests that this issue has been addressed via exclusions, with some studies dropping individuals with terminal illness or mortality within one year. However, this attempt still fails to account for 5 and 10 year mortalities due to comorbidity. Table 1 regression models, which depict the association between LDL-C and all-cause and CVD mortality, exhibit an absence of adequate accounting for comorbidities(1). An overwhelming majority of studies do not include significant non-cardiovascular conditions (e.g. COPD, cancer, rheumatologic disease, liver disease, etc.), nor the stage or severity of such disorders. Additionally, other comorbidities, such as frailty, which is associated with malnutrition and mortality, are not adequately accounted for. Failure to find the expected risk associations with cholesterol in the elderly is consistent with epidemiological bias.
These biases may be dealt with, to some extent, by considering genetic predisposition to hyperlipidemia (via Mendelian randomization). In this respect, the article fails to include a study by Postmus et al. showing that a genetic disposition to high LDL-C levels contributes to mortality throughout life, including the oldest elderly, and an advantageous genetic disposition contributes to low LDL-C with familial longevity(6).
Additionally, the exclusions of the study are insufficient. The article claims to have "excluded studies without multivariate correction for the association between LDL-C and all-cause and/or CV mortality." However, Table 2 shows factors corrected for in the multifactorial analyses of each study and in the study by Bathum et al., specific factors corrected for were not stated, thereby providing insufficient evidence to conclude whether such corrections were made or not. Importantly, the Bathum et al. study was by far the largest, including 68,085 participants, constituting about two-thirds of the systematic review. Therefore, the majority of this data may be invalid simply based off this study's own stated eligibility criteria.
Furthermore, the study did not consider the use of statins among participants. This is a major flaw since it is likely that middle aged and elderly people with high LDL-C will receive statins. Given that statins are known to reduce all-cause mortality, and those with higher LDL-C will be most likely to receive statin therapy, this will make the group with higher baseline LDL-C not appear as high risk because the risk has already been treated.
Both the UK-NICE guidelines and the 2013 ACC-AHA guidelines are based off high quality, randomized controlled trial data, and strongly endorse the use of statins in appropriately selected patients. In individuals aged 40-75, the 2013 ACC/AHA guidelines identify 4 statin benefit groups where randomized controlled trial data supports net benefit, and the guidelines advise reviewing the suitability of a prescription in a clinician-patient risk discussion. Above 75 years of age, statins are not routinely recommended for prescription in primary prevention, but could be indicated if a clinician-patient risk discussion felt that this was clinically appropriate. The ACC-AHA cholesterol guidelines stress the importance of clinician guidance that emphasizes lifestyle, addresses other risk factors, and evaluates the potential for benefit and for adverse effects. Both the UK-NICE and ACC/AHA cholesterol guidelines also advise clinicians to evaluate who would not benefit from statins(2,3).
We write this letter because a debate that truly benefits public health and well-being requires use of critically gathered evidence. "Lack of an association or an inverse association between low-density- lipoprotein cholesterol and mortality in the elderly: a systematic review" fails to analytically discuss the best evidence, and raises the concern that the misguided conclusions will harm implementation of cholesterol guidelines in both the UK and the United States. These guidelines adhere closely to critically evaluated, high quality evidence that will improve people's health. In contrast, the present poor quality study confuses readers more than it enlightens. Major flaws in methodology include lack of understanding of major national health guidelines, of selection and survivor bias, of adjustment inclusions and exclusions, and of consideration of statin use.
To argue successfully against mainstream ideology, one's conclusions must stem from skepticisms that are logical, rational, and valid. Unfortunately, the present article does not meet these criteria. The article's inappropriate conclusions jeopardize the opportunity to pursue current evidence-based guidelines that endorse cost-effective healthcare practices(7). The serious flaws of the article also elicit a need for examination of the responsibilities of media and medical journals, such as BMJ Open, when publishing papers that confront topics with potentially health-altering and life-affecting ramifications. The scientific community and the public both deserved a more critical peer review of the article and subsequently appropriate revisions before it was published.
1. Ravnskov U, Diamond DM, Hama R, Hamazaki T, Hammarskjold B, Hynes N, Kendrick M, Langsjoen PH, Malhotra A, Mascitelli L, McCully KS, Ogushi Y, Okuyama H, Rosch PJ, Schersten T, Sultan S, Sundberg R. Lack of an association or an inverse association between low-density-lipoprotein cholesterol and mortality in the elderly: a systematic review. BMJ Open, 2016 Jun 12;6(6):e010401.
2. Stone NJ, Robinson JG, Lichtenstein AH, Bairey Merz CN, Blum CB, Eckel RH, Goldberg AC, Gordon D, Levy D, Lloyd-Jones DM, McBride P, Schwartz JS, Shero ST, Smith SC Jr, Watson K, Wilson PW. 2013 ACC/AHA guideline on the treatment of blood cholesterol to reduce atherosclerotic cardiovascular risk in adults: a report of the American College of Cardiology/American Heart Association Task Force on Practice Guidelines. J Am Coll Cardiol, 2014 Jul 1;63(25 Pt B):2889-934. Erratum in: J Am Coll Cardiol, 2015 Dec 22;66(24):2812. J Am Coll Cardiol. 2014 Jul 1;63(25 Pt B):3024-3025.
3. National Clinical Guideline Centre (UK). Lipid Modification: Cardiovascular Risk Assessment and the Modification of Blood Lipids for the Primary and Secondary Prevention of Cardiovascular Disease. London: National Institute for Health and Care Excellence (UK), 2014.
4. Ridker, PM. LDL cholesterol: controversies and future therapeutic directions. Lancet, 2014 Aug; 384(9943):607-617.
5. Robinson, JG, Stone NJ. Identifying patients for aggressive cholesterol lowering: the risk curve concept. Am J Cardiol, 2006 Nov 15;98(10):1405-8. Epub 2006 Oct 2.
6. Postmus I, Deelen J, Sedaghat S, Trompet S, de Craen AJ, Heijmans BT, Franco OH, Hofman A, Dehghan A, Slagboom PE, Westendorp RG, Jukema JW. LDL cholesterol still a problem in old age? A Mendelian randomization study. Int J Epidemiol, 2015 Apr;44(2):604-12. Epub 2015 Apr 7.
7. Greenland P, Lauer MS. Cholesterol Lowering in 2015: Still Answering Questions About How and in Whom. JAMA, 2015 Jul 14;314(2):127-8.
Use optimal doses for optimal results
I read with interest the design of this game-changing proof-of-concept study.The designers of the trial deserve congratulations. However, I have a few suggestions to tender:
1. The dose of Vit D used in the study is unequivocally sub-optimal (1000 IU/D); in VITAL study,1 2000 IU/D is used. In fact VITAL was criticized because of rather less doses.
2. If we are not measuring baseline Vit D level, it may be better to use maximal (4000 IU/D) or submaximal dose (3000 IU/D), as most patients have either deficiency or insufficiency of Vit D or first to measure the baseline Vit D level (as now it is commonly conducted in the clinical practice), if found low, to be corrected and then the maintenance dose 1000 IU/D (as used in the study)or still better 2000 IU/D is used. This will avoid the under-dosing of Vit D, a common mistake in the clinical trials (from our past experiences, may be because of fear of overdosing), leading to negative results in almost all interventional trials conducted with Vit D so far.
3. Why to include patients following invasive revascularization (PCI) only, as still most patients with STEMI do not get PCI. In fact, such patients have more adverse remodeling. This is to improve the external validity of this excellent and timely study.
1.Manson JE, Bassuk SS, Lee IM, et al. The VITamin D and OmegA-3 TriaL (VITAL): rationale and design of a large randomized controlled trial of vitamin D and marine omega-3 fatty acid supplements for the primary prevention of cancer and cardiovascular disease. Contemp Clin Trials, 2012;33:159-71.
Conflict of Interest:
The Possible Association of the Incidence of ESRD in the Patient with Diabetic Nephropathy with Salt Intake in the World
Increasing number of the patients with endstage renal disease (ESRD) is nowadays a serious problem in each country, including many Western countries and Asian countries. Diabetic nephropathy (DMN) is the major cause of the incidence of ESRD in worldwide. In Japan, DMN has been the leading cause of dialysis since 1998 despite many innovative achievements in the pharmacological treatment for diabetes mellitus. Excessive salt intake causes hypertension and increases the risk for cerebro-cardio- vascular disease as well as ESRD . However, the association of salt intake and the incidence of ESRD in the patients with DMN remains unknown. It is reported that many Asian countries, such as Singapore, Malaysia, Republic of Korea, Hong Kong, Taiwan, Philippines and Japan, head the list of the percentage of incident patients of ESRD due to diabetes . Meanwhile, many Western countries, such as United States, Iceland, Canada, Finland, Portugal, Croatia, Czech Republic, Austria, Greece, Denmark, Bosnia/Herzegovina, United Kingdom, Sweden, Spain, Scotland, France, Serbia, Belgium, Netherlands, Norway and Romania, run after Asian countries. A report of global national sodium intakes shows that these East Asian countries consume more salt than these Western countries . We simply analyzed the relationship between percent incidence of DMN in ESRD and salt intake(Figure, not shown). It clearly demonstrated a significant relationship between them (r = 0.483, P = 0.009). The average percent incidence of DMN in ESRD in East Asian countries was significantly higher than that in Western countries (47.5 % vs 27 %, p < 0.001) as well as salt intake (11.8 g/day vs 9.5 g/day, p < 0.001), suggesting the link between progression of DMN and salt intake in East Asian countries, while the protection of DMN by low salt consumptions in Western countries. A multiple linear regression analysis adjusted by salt intake demonstrated that the average percent incidence of DMN in ESRD in East Asian countries was still significantly higher than that in Western countries (p < 0.001). The result indicated that DMN patients in East Asian countries are genetically salt-sensitive compared with Western countries. A few reports supported the idea that there is a certain difference of salt sensitivity between East Asian and Western countries . Further studies are required to confirm the association of the incidence of ESRD in the patients with DMN and salt intake.
1. Mozaffarian D, Fahimi S, Singh GM, et al. Global sodium consumption and death from cardiovascular causes. N Engl J Med 2014;371:624-34.
2. U S Renal Data System. USRDS 2013 Annual Data Report: Atlas of Chronic Kidney Disease and End-Stage Renal Disease in the United States. Bethesda, MD: National Institutes of Health, National Institute of Diabetes and Digestive and Kidney Diseases; 2013.
3. Powles J, Fahimi S, Micha R, et al, Global, regional and national sodium intakes in 1990 and 2010: a systematic analysis of 24 h urinary sodium excretion and dietary surveys worldwide. BMJ Open, 2013, 3:e003733.
4.Mente A, O'Donnell MJ, Rangarajan S, et al. Association of urinary sodium and potassium excretion with blood pressure. N Engl J Med 2014;371:601-611
Conflict of Interest:
Blood transfusion: a double-edged sword
I read with interest the article. Though blood transfusion is life- saving in patients with massive bleed, its routine use like transfusion in post-operative patients with Hb <10 gm% is definitely counter- productive.The transfusion of even as little as 1 unit of RBCs has been associated with decrease 10-year survival after CABG.(1,2)
1. Koch CG,Duncan AI, Mihalijevic T, et al.Transfusion in coronary artery bypass grafting is associated long-term survival. Ann Thorac Surg.2006;81:1650-1657.
2.Murphy GJ, Reeves BC, Rogers CA, Rizvi SI, Culliford L, Angelini GD. Increased mortality, postoperative morbidity, and cost after red blood cell transfusion in patients having cardiac surgery. Circulation. 2007;116:2544-2552.
Conflict of Interest:
Effectiveness of the Assessment of Burden of COPD (ABC) tool on health-related quality of life in patients with COPD: Twitter Discussions from the University of Toronto Respirology and Sleep Journal Club (@respandsleepjc)
Preyanka Abhyankar, Anju Anand, Matthew B. Stanbrook
We welcomed the study by Slok and colleagues examining the effect of a tool for assessing the burden of COPD on quality of life as the article of discussion for our Twitter-based asynchronous monthly respirology and sleep journal club. This non-blinded cluster randomized control trial included both primary and hospitalist care and found that the Assessment of Burden of COPD (ABC) tool produced improvements on two separate quality of life measures (SGRQ, PACIC) but not on a third measure (the CAT) (1).
The most important issue identified in our online discussions was the potential that the main results could be an artefact of regression to the mean. The intervention and control groups differed at baseline, both with regard to baseline disease severity as reflected by FEV1 and FEV1/FVC ratio, as well as in the baseline values of the quality of life outcome measures. Post-intervention, the two groups became progressively more similar over time, as illustrated in Table 2. Thus, rather than a true effect of the intervention, the study results could simply reflect natural variation around a common mean level of disease- specific quality of life with the intervention group, showing the greatest response only because they happened to diverge furthest from this level at baseline (2,3). It was unclear if the groups were unbalanced due to cluster randomization itself or due to the real-world nature of the study not lending itself well to randomization, which was further exacerbated by the small sample size (4,5).
Another important issue highlighted in our discussions was that this study was unblinded or and lacked a sham group. Compounded with the subjective nature of the outcome measure, this may have introduced reporting bias (6). The study's inability to capture more objective lung function and exacerbation outcomes as planned is thereby even more problematic, and as a result our group felt that it is difficult for the study to yield a meaningful evaluation of the ABC tool (7).
A final issue raised was that the study was performed under real- world conditions, which can be an asset, however the liberal inclusion criteria (e.g. including any obstructive lung pathology with FEV1/FVC < ,0.7, not requiring a smoking history, etc.) raised concern around misclassification of patients (8,9).
We do agree with Slok et al. that developing and validating patient care interventions like the ABC tool is an important step towards enhancing patient involvement in the management of their chronic illness and we commend the efforts of the authors to do so via a randomized trial. However, we feel further studies are still needed to assess the effectiveness of this tool before it becomes clear what value it may hold for clinical practice (10, 11).
REFERENCES 1. Slok, A. H., Chavannes, N. H., van der Molen, T., Rutten-van M?lken, M. P., Kerstjens, H. A., Salom?, P. L., ... & van Schayck, O. C. (2014). Development of the Assessment of Burden of COPD tool: an integrated tool to measure the burden of COPD. NPJ primary care respiratory medicine, 24, 14021. 2. Stanbrook, M. [drstanbrook]. (2016, Jul 21). @respandsleepjc Take a look at table of continuous SGRQ scores. Clear evidence of regression to the mean. This is all an artefact. #rsjc [Tweet]. Retrieved from https://twitter.com/drstanbrook/status/756268723980292096 3. Stanbrook, M. [drstanbrook]. (2016, Jul 22). @respandsleepjc Still a problem. Intervention got better while control got WORSE = RTTM. #rsjc https://t.co/JG77Qub5Az [Tweet]. Retrieved from https://twitter.com/drstanbrook/status/756278596495368193 4. Vagaon, A. [AndreiV_Resp]. (2016, Jul 21). @respandsleepjc Perhaps an effect of the real world not randomizing in a good way; ?smaller sample more prone; but throws things off #rsjc [Tweet]. Retrieved from https://twitter.com/andreiv_resp/status/756271906786074625 5. Christiansen, D. [dcwpg]. (2016, Jul 21). Unusual to see groups so unequal at baseline. Is it a result of the clustered randomization and having too few study docs? #rsjc [Tweet]. Retrieved from https://twitter.com/dcwpg/status/756270239516467201 6. Stanbrook, M. [drstanbrook]. (2016, Jul 21). @respandsleepjc Not good enough. This is an unblinded trial with a subjective outcome measure. Setup for bias. #rsjc https://t.co/Wph3qMC7F2 [Tweet]. Retrieved from https://twitter.com/drstanbrook/status/756266741462728704 7. Zaheen, A. [drazaheen]. (2016, Jul 22). @respandsleepjc But difficult to comment on the value of ABC in the absence of objective data! #rsjc [Tweet]. Retrieved from https://twitter.com/drazaheen/status/756278274444005378 8. Christiansen, D. [dcwpg]. (2016, Jul 21). Great to see an RCT done under real-world conditions. Struck by the very liberal inclusion criteria (didn't even require a smoking Hx) #rsjc [Tweet]. Retrieved from https://twitter.com/dcwpg/status/756265754329092096 9. Vagaon, A. [AndreiV_Resp]. (2016, Jul 21). @thelungdr Not sure why absolute ratio 0.7, rather than LLNs. Ptnt can be misclasified. Esp. as impact was 49 v 33 people @ 18 months #rsjc [Tweet]. Retrieved from https://twitter.com/andreiv_resp/status/756268872781664256 10. Anand, A. [respandsleepjc]. (2016, Jul 22). Summary- interesting study - grp not bal to start, blinding (lack of) & RTTM problematic-- need more studies to assess this tool #rsjc [Tweet]. Retrieved from https://twitter.com/respandsleepjc/status/756285601477980160 11. Zaheen, A. [drazaheen]. (2016, Jul 22). @respandsleepjc Part of the important trend towards patient involvement in the management of chronic illness #rsjc [Tweet]. Retrieved from https://twitter.com/drazaheen/status/756277959481143296
Conflict of Interest: