Having read the article by Stylianou, Buchan & Dunn  reviewing the International Burn Injury Database we have concerns regarding conflicts of interest, failure to acknowledge the contribution of burns services and also the interpretation of the data presented. The senior author failed to disclose that he has been directly involved in the development of the database, was involved in making it a mandatory part of burns care in England and is currently paid to manage it. In another online BMJ publication Injury Prevention , the same senior author gave his affiliation as: International Burn Injury Database, Burn Centre, Acute Block UHSM Southmoor Road, Manchester M23 9LT, UK. He is also chairman of the Burn Care Informatics Group which is supposed to oversee the development and use of iBID. We are unclear how the latter group can function with any independence when the chair of that group is also responsible for the running of the database itself and also authoring articles based on the entirety of that data. All burns services contribute to the database and this has required significant efforts at considerable cost to ensure that data is collected accurately and in a timely fashion. Without this contribution, iBID would have little data and acknowledging this would also have been appropriate.
iBID is funded by the NHS with direct and indirect costs, none of which have ever been published or are easily available. The direct costs are noted...
iBID is funded by the NHS with direct and indirect costs, none of which have ever been published or are easily available. The direct costs are noted in official documents in our possession to be around £275,000 of which a portion is allocated to wages including the senior author via sessions remunerated from iBid funds administered by the hosting Manchester NHS service. In order to be transparent, we feel it is important for readers to be aware of this, especially when one of the conclusions of the paper is that iBid should be mandatory. The indirect costs are likely to be considerably more because every burns service requires data input clerks for the sole purpose of mandatory iBid data entry, and all members of the multidisciplinary team to contribute to data acquisition. Whilst staff costs are therefore difficult to fully define as the time given by all staff is difficult to measure, and because none of these figures have been published, we can estimate the indirect costs of data entry. Using figures from our own services and translating them across all services, a conservative estimate is £15,000 per year per burns service to employ data clerks which translates to an estimate of indirect costs of be £545,000 but likely to be much more. We would welcome a piece of work that finally publishes the exact figures for direct and indirect costs at a time of funding concerns, as well as published annual accounts capturing all the costs as we all need to be clear about the tangible benefits of such an investment. Costs of running any database can be high but for a relatively small specialty we therefore estimate at least £820,000 a year is spent on acquiring data which translates to £7.3 million for the time-period during which the data upon which this paper relies was collected. Importantly, these costs were born by all burns services across the country who subsequently had no input into the authorship of the paper in question, and in our view are likely to have made different conclusions to those made by the authors.
Data of this kind should be of use to commissioners and clinicians alike, but the presentation of such data raises concerns, especially when some data translates into dashboards upon which service performance is judged and comparisons made. The conclusion made by the authors that there has been up to a threefold increase in burns activity is dangerously inappropriate when one considers the introduction of any database. Although they acknowledge that slow uptake and increased data entry of non-admitted burns has contributed to the rise in their discussion, we feel that there are many flaws in the way that they have presented their results. Suggesting that a rapid rise of data records is coincident with increased clinical activity when a new mandatory database has been introduced is not the most likely cause. Our own experience is reflected by others who note that the introduction of a new process was challenging and took one or more years to fully integrate. This may also have an impact on geographical locations of burns, as services which have been using the database longest may end up recording higher numbers. A number of other conclusions such as "The [Trust] with the highest workload [in the UK is] the Manchester Teaching PCT" (to which the authors are affiliated and which hosts the database) are also deeply flawed, especially as commissioning decisions might well be made based on such conclusions.
The authors report "admissions" and "workload" but fail to identify one of the major concerns with iBID: there are no clear definitions in iBID relating to any of the common data points resulting in significant variations in what is recorded. This means that one service can record an admission while exactly the same patient may be recorded as an out-patient as each service defines an admission differently. This is also the case for many other data fields meaning that comparison between services is not easily possible. Furthermore, each service may choose to only record burns which are admitted rather than all of the cases referred to the service. This variation in recording types of cases may also skew any interpretation of geographical variation. The authors also briefly mention data cleaning and data completeness. We have concerns that they do not clearly define what they mean by data cleaning as this may significantly alter the output of any database. Again, data completeness may have a significant impact on any output depending on what limits are applied when developing a report. Even if the database adapts and improves in future, or has started to do so, this will not affect or improve all previous years of data upon which the conclusions of this paper have relied.
These points have been raised by the burns community for several years and up until recently we did not have access to the way data fields were used to produce reports to ensure that they could be reproduced by others. These concerns still remain. This is exampled by some data generated by iBid relating to inhalation injury where there seems to be a cohort of patients not admitted to hospital, yet who sustained moderate or severe inhalation injury (requiring mechanical ventilation) - which in practice is clearly not compatible. Concerns have also been raised within the NHS regarding various aspects of iBID including its ability to provide reliable and useful data . These concerns have led to the decision by the National ODN Group* (of which we are current or past members) representing all four Burn Networks not to use national iBid data reports for the National Burns Mortality Audit.
The authors believe that iBID should only continue as a mandatory database if the concerns raised and the limitations expressed have been fully addressed through an independent process that allows complete transparency with regards to governance and data quality ensuring that those who are directly involved with the database have no conflicts of interest. 21st century medicine often quotes the benefits of data but without ensuring that the quality of reports from such data are able to have a direct impact on care we advise caution. We would encourage the authors to share their raw data as promised in their initial paper to allow others to try and reproduce their reports and also to take a more balanced interpretation of the data they present as well as present a more comprehensive view of the limitations of their work.
We also note that the declared source of funding for this project was stated to be the Margaret Miller Fund, which we understand to be restricted funds for the sole purpose of ‘research into methods of preventing burn injuries in the home’, and to which this research does not appear to relate.
1. Neophytos Stylianou, Iain Buchan, Ken W Dunn. A review of the international Burn Injury Database (iBID) for England and Wales: descriptive analysis of burn injuries 2003–2011.
2. K Dunn. The epidemiology and continued monitoring of burn injury in England and Wales. P Safety 2010 abstracts. Injury Prevention 2010;16(Suppl 1):A1–A289. DOi: 10.1136/ip.2010.029215.753
3. Informing the future procurement of the International Burn Injury Database (iBID) HQIP 2011.
Keywords: iBid, database, data, burns, conflicts of interest, audit
Affiliations, Statements and Disclosures:
At the time of writing
Kayvan Shokrollahi FRCS(Plast) LLM is the Clinical Lead for the Northern Burn Operational Delivery Network*, NHS England; Clinical Lead for the Mersey Regional Burns Service; Vice-Chairman of the Charity The Katie Piper Foundation; Editor-in-Chief of the Journal Scars Burns & Healing; Associate Editor of the Journal Annals of Plastic Surgery; Chairman of the Communications Subcommittee of the British Burn Association.
Baljit Dheansa FRCS(Plast) has recently stepped down as the Clinical Lead for the South East of England Burn Operational Delivery Network*, NHS England and is Lead for Burns at Queen Victoria Hospital East Grinstead.
William Dickson MBE FRCS(Glas) FRCS (Eng) is the Adult Clinical Lead for the South West UK Burn Operational Delivery Network*, NHS England, and formerly Director of the Welsh Burns Centre, Morriston Hospital, Swansea.
*There are 4 burn networks covering the whole of England comprising North, Midlands, South East and South West operational delivery networks (ODNs). The Managers and Clinical Leads of each plus commissioners constitute the National ODN group.
The problem is the method used in practice for the selection of variables to be included in logistic regression and Cox models in observational medical studies.
The motivation comes from the authors’ work as statistical consultants. Many medical researchers had the idea that only variables which were individually significant should be included in the fitted model. This is in contrast to the correct procedure in which the model should contain variables that are jointly significant. To find these models requires fitting several models and selecting the best, rather than fitting just one. An example is in Table 1 below.
The paper presents the results of a survey in which the frequency of an incorrect method of variable selection was measured as a function of the assessed statistical expertise of the authors of the papers: first author, any other author or none. The expertise was based on the authors’ departmental affiliations. It was found that the frequency of correct variable selection increased with the statistical qualifications of the authors. Clinical trials, as opposed to observational studies, were not included.
The authors also consider how the situation might be improved. A breakdown of the results by country from papers in which the first author is not an expert shows North America and Northern Europe show relatively high expert involvement compared with East Asia, which have a lower involvement. Taiwan is an exception. In the authors’ own cou...
The authors also consider how the situation might be improved. A breakdown of the results by country from papers in which the first author is not an expert shows North America and Northern Europe show relatively high expert involvement compared with East Asia, which have a lower involvement. Taiwan is an exception. In the authors’ own country of Japan the education of biostatisticians is developing rapidly. However, it will take time to develop well-trained experts and this is only in one country. The authors suggest that data be made available and analyzed as part of the peer review process. Such suggestions have been made before, for example in power calculations in grant proposals. It would be excellent if some such system could be made to work. Unfortunately, statistical referees are busy and the standard of reviewing of statistical papers seems to be deteriorating not improving.
In their Supplementary Table 3 the authors present an example of a logistic regression analysis which illustrates the consequences of the incorrect procedure using inference on one factor at a time. The results of the proper analysis are also given. I summarise this analysis in Table 1. There are three factors:
• A: adjuvant chemotherapy
• L: Lymph node metastasis
• B: Biomarker positive
The three left-hand columns of the table indicate the factors included in the model and the right-hand columns indicate the significant variables. Seven models are fitted. The first three rows show the results of fitting the three one-factor models: L and B are individually significant, but not A. For the three two-factor models, L and B and A and L are both significant, but when A and B are fitted, only B is significant. However, as the last row of the table shows, when all three factors are included, all are significant.
Table 1, available at https://bit.ly/2rIucUh: Significance of factors when seven different models are fitted to logistic regression analysis of hypothetical data on recurrence of cancer after surgery.
The example shows that all three variables need to be fitted in order to obtain the best model. In other examples only some of the factors may be required. But several models have to be fitted to determine which best describes the data. Such tables can be amplified by using one or more asterisks to express significance levels and by adding an extra column for some overall measure of fit.
In their discussion section the authors also mention problems that arise with few data and several factors. In this case again several models should be assessed, although it will not be possible to fit a full model like that in the last row of Table 1. However a similar table may be helpful in assessing the properties of the various fitted models, perhaps augmented by a measure of model adequacy such as the information criterion AIC.
We read with great interest the comprehensive review of primary care consultation duration in 67 countries between 1946 and 2016 by Irving et al (1). This review is especially timely given rising physician burnout, as well as dissatisfaction among both doctors and patients in the U.S. As the authors note, many physicians are frustrated by the limited time available to interact with patients.
The increasing time of U.S. physicians with patients surprised us. Primary care physicians in the U.S. rank fifth out of ten high-income countries on dissatisfaction with time spent per patient (2). What explains this apparent mismatch of quantitative trends and satisfaction?
One candidate explanation is that much of physician time is spent on activities other than communication with patients. According to an observational study in 2015 of 57 ambulatory care physicians (primary care, cardiology, and orthopedics) in 16 practices in 4 states, of time spent with patients in the exam room, 53% was spent face-to-face, 37% on the electronic health record (EHR) and desk work, and 9% on administrative tasks (3).
Thus, we wondered if the U.S. trend in primary care consultation duration reported by Irving et al aligned with historical trends in EHR uptake. In the Figure (http://blogs.bmj.com/bmjopen/files/2018/05/Figure-US-Primary-Care-Consul.....
Thus, we wondered if the U.S. trend in primary care consultation duration reported by Irving et al aligned with historical trends in EHR uptake. In the Figure (http://blogs.bmj.com/bmjopen/files/2018/05/Figure-US-Primary-Care-Consul...) we compare these two temporal patterns. Examination of the Irving data suggest to us two time periods with different slopes: nearly flat from 1992-2004, and then rising from 2004-2012. The rising period aligns well in time with rising EHR uptake (4). Although comparison of these two trends is only suggestive, we believe it provides strong cautionary evidence against interpreting the rise in consultation duration as a rise in physician-patient communication.
Physicians do not view the increasing EHR burden favorably. The ambulatory care study noted above found that physician satisfaction results from providing high quality medical care and caring for patients, while EHR/desk work and the complexity of reimbursement and administrative tasks contribute to dissatisfaction (5). Physician satisfaction with the EHR is far lower in the U.S. (52%) than in eight other wealthy nations (64% to 86%) (2).
While these issues are beyond the scope of Irving et al’s review, we believe that attention must be focused on primary care consultation duration that entails undisturbed communication with the patient, absent attending to the computer. This time is central to caring for patients and its continual undermining is a risk to the health of both patients and physicians.
1. Irving G, Neves AL, Dambha-Miller H, et al. International variations in primary care physician consultation time: a systematic review of 67 countries. BMJ Open. 2017; 7(10):e017902. doi:10.1136/bmjopen-2017-017902.
2. Osborn R, Moulds D, Schneider EC, Doty MM, Squires D, Sarnak DO. Primary Care Physicians In Ten Countries Report Challenges Caring For Patients With Complex Health Needs. Health Aff (Millwood). 2015 Dec;34(12):2104-12. doi: 10.1377/hlthaff.2015.1018.
3. Sinsky C, Colligan L, Li L, et al. Allocation of Physician Time in Ambulatory Practice: A Time and Motion Study in 4 Specialties. Ann Intern Med 2016;165(11):753-760.
4. Hsiao C-J, Hing E, Ashman J. Trends in Electronic Health Record System Use Among Office-based Physicians: United States, 2007–2012. National Health Statistics Reports, No. 75, May 2014.
5. Colligan L, Sinsky C, Goeders L, Schmidt-Bowman M, Tutty M. Sources of physician satisfaction and dissatisfaction and review of administrative tasks in ambulatory practice: A qualitative analysis of physician and staff interviews. October 2016. Available at: ama-assn.org/go/psps.
Note that the emphasis in this paper is on the amount of change after implementing the diets rather than the more important absolute values.
Adding 50g of fat to a diet already high-fat diet is not a healthy dietary modiﬁcation. All three diets were 36-37% fat (by energy) which is higher than the US average of 33%.
The average total cholesterol for all diets at the start of the trial was 5.9-6.0 mmol/L – which is very high. The cholesterol was high at the start of the trial and was still high at the end. The Framingham Risk Assessment accumulates risk points at 160 mmol/dL (4.0 mmol/L) or greater for total cholesterol.
Total cholesterol was raised for coconut oil (mean 0.22) and butter (mean 0.59). The average increase for olive oil was much less (mean 0.03). The standard deviation was higher for coconut oil and butter compared with olive oil (0.55, 0.59, 0.43).
The baseline values for fasting glucose was 5.3-5.4 mmol/L. A frequently quoted reference range is 3.6-6.0 mmol/L although a reasonable desirable level is lower at 3.9-5.0 mmol/L. After 4 weeks, the fasting glucose was decreased an average of 0.05 mmol/L for coconut oil, raised 0.02 mmol/l for butter and decreased 0.06 mmol/L for olive oil. These are not a significant beneficial outcomes.
Systolic blood pressure is also high. Optimal systolic blood pressure is less than 120. Coconut oil had a greater tendency to raise the systolic blood pressure compared to butter and olive oil....
Systolic blood pressure is also high. Optimal systolic blood pressure is less than 120. Coconut oil had a greater tendency to raise the systolic blood pressure compared to butter and olive oil.
Not all authorities agree that HDL cholesterol is a valid indicator of cardio-vascular health. The fact that coconut oil raised HDL cholesterol is not relevant to better health outcomes.
A change in cholesterol is not the only impact that a high-fat diet and high saturated fat diet has on health.
High-fat diets have a multitude of adverse health outcomes.
A single high-fat meal has a signiﬁcant impact on endothelial function which takes several hours to recover – just in time for your next high-fat meal. This impacts arterial elasticity and blood flow  as well as increasing inflammation. 
Another study  concluded, “that even a single high-fat meal may be associated with heightened cardiovascular reactivity to stress”.
The ﬂuidity of the cell membranes is decreased and the permeability is increased with an increase of saturated fats, as well as increasing the viscosity of the blood and increasing the adhesiveness of blood cells.
The conclusion of this paper stated, “these findings do not alter current dietary recommendations to reduce saturated fat intake in general but highlight the need for further elucidation of the more nuanced relationships between different dietary fats and health.”
Given the lack of any health benefits in the three diets examined, it is difficult to conclude that a “more nuanced” approach will result in a better understanding of the relationships between dietary fats and health.
A number of researchers studied the relationship of saturated fat to serum cholesterol during the 1950s. J Groen, LW Kinsell, EH Ahrens, A Keys, JM Beveridge and B Bronte-Stewart replaced saturated fats in the diet with polyunsaturated fats. All other components of the diet remained the same and the total fat content of the diet did not change.
When the unsaturated fats, such as corn or safflower oil, were replaced by the saturated fats of butter, lard, or coconut oil, the serum cholesterol rose. The serum cholesterol fell when the polyunsaturated fats were reintroduced. The experiments were repeated, and whilst there was variability with the amount of change for different individuals, the results were consistent for each individual. The changes occurred rapidly within one or two weeks.
Unfortunately, Dr Michael Mosley (Trust Me, I’m a Doctor) used the results of this study to conclude that “coconut oil may be good for you”. 
* * * * *
 Roberts, W. C. (2010) It’s the cholesterol, stupid! American Journal of Cardiology. 106 (9), 57–73.
 Vogel, R. A. et al. (1997) Effect of a Single High-Fat Meal on Endothelial Function in Healthy Subjects. American Journal of Cardiology. 79 (3), 350–354.
 Esposito, K. et al. (2007) Effect of a single high-fat meal on endothelial function in patients with the metabolic syndrome: role of tumor necrosis factor-α. Nutrition, metabolism and cardiovascular diseases. 17 (4), 274–279.
 Jakulj, F. et al. (2007) A high-fat meal increases cardiovascular reactivity to psychological stress in healthy young adults. The Journal of nutrition. 137 (4), 935–939.
 Noone, Y. (2018) Why Dr Michael Mosley now thinks that coconut oil may be good for you [online]. Available from: https://www.sbs.com.au/food/health/article/2018/02/26/why-dr-michael-mos....
As a Rehabilitation Psychologist who has seen the remarkable effects of psychologist involvement with critically ill patients or recently critically ill patients, and their families, I continue to read articles like this with feelings of bafflement and sadness. The PERSON and their FAMILY have so much to understand and process, and a good psychologist who is informed and experienced regarding these challenges can do SO MUCH good in helping better participation, better comprehension, better discharge planning. Also, very much of the variance in patients' responses to care and rehabilitation stems from residual or recurring delirium or sub-syndromal delirium, as well as lingering cognitive deficits not attributable to current delirium. Psychologists and Nurses are ideal partners in monitoring and responding to delirium. And, patients and families respond VERY WELL to basic education about delirium. Even patients with fluctuating mental status can retain some information about delirium so that when their thinking clouds again they react with less suspicion, paranoia and shame. . And they can process later what has happened, and can report incipient symptoms to their Nurses. PLEASE consider how to bring Psychologists on board with teams on ICUs and step down units. And please listen to the ones already working in rehabilitation, including acute and subacute settings. Thank you.
We thank the reader for identifying these errors and a correction to the article will be published shortly.
We recently read with great interest an article entitled “Association between exposure to the Chinese famine during infancy and the risk of self-reported chronic lung diseases in adulthood a cross-sectional study, ” by Zhenghe Wang(2017) in BMJ Open 7(5), e015476.The authors examine the association between early-life exposure to the Chinese famine and the risk of chronic lung diseases in adulthood. This study makes a worthy contribution to the area. However, some issues should be taken into account.
In the paper, there are some mistakes in the figure 1 which named “Flowchart on the sample selecting methods at each step”, Combine the context, the number of non-exposed(855)、fetal-exposed(830)、infant-exposed(568)、preschool-exposed(630) groups are wrong in the second line from the bottom. We would like to bring to your attention the errors in methods reported in the aforementioned article.
We are delighted to read the misleadingly entitled letter by Karapanagiotidis and Grigoriadis, as it gives us the opportunity to present additional convincing evidence gathered after publication in favor of the pathogenicity of the D313Y GLA mutation. It might also be noted that Karapanagiotidis and Grigoriadis refer to only two of the reported cases, disregarding the strong supporting evidence provided by the study of the other cases. Obviously, their objections come from the fact that they were restricted to the neurological approach to Patient 4 (thus their mention in the Acknowledgements of our paper), underestimating her nephrological profile, which is not even mentioned in their letter. Taking into account that, one year after the last stroke, the patient presented with microalbuminuria that was duplicated after 3 months, as was mentioned in our paper, we proceeded to renal biopsy. On electron microscopy, typical signs of Fabry disease were detected, i.e. podocyte injury, significant cytoplasmic vacuolization of podocytes with a mild presence of sphingolipids and myelin bodies in podocytes and tubular cells. According to the current diagnostic criteria, these findings confirm the definite diagnosis of Fabry disease in patients with “genetic variants of uncertain significance and non-specific FD signs” (Biegstraaten et al, Orphanet J Rare Dis 2015). Additionally, in a recent ophthalmological assessment, this patient presented with signs of "cornea verticillata...
We are delighted to read the misleadingly entitled letter by Karapanagiotidis and Grigoriadis, as it gives us the opportunity to present additional convincing evidence gathered after publication in favor of the pathogenicity of the D313Y GLA mutation. It might also be noted that Karapanagiotidis and Grigoriadis refer to only two of the reported cases, disregarding the strong supporting evidence provided by the study of the other cases. Obviously, their objections come from the fact that they were restricted to the neurological approach to Patient 4 (thus their mention in the Acknowledgements of our paper), underestimating her nephrological profile, which is not even mentioned in their letter. Taking into account that, one year after the last stroke, the patient presented with microalbuminuria that was duplicated after 3 months, as was mentioned in our paper, we proceeded to renal biopsy. On electron microscopy, typical signs of Fabry disease were detected, i.e. podocyte injury, significant cytoplasmic vacuolization of podocytes with a mild presence of sphingolipids and myelin bodies in podocytes and tubular cells. According to the current diagnostic criteria, these findings confirm the definite diagnosis of Fabry disease in patients with “genetic variants of uncertain significance and non-specific FD signs” (Biegstraaten et al, Orphanet J Rare Dis 2015). Additionally, in a recent ophthalmological assessment, this patient presented with signs of "cornea verticillata" ophthalmopathy onset, a characteristic mark of the disease. Further, the mother of this patient (Patient 5), initially misdiagnosed as a multiple sclerosis patient, not only carries the same GLA mutation but also suffers multiple white matter lesions and pains in the extremities of undetermined etiology, and thus is also diagnosed with Fabry disease.
Consequent to the above, the “misunderstandings” in our paper to which Karapanagiotidis and Grigoriadis refer in their letter, such as the supposed use of Gb3s or the use of genotype-phenotype correlations as diagnostic criteria, are not worthy of comment.
We can only agree, however, with the implication of Karapanagiotidis and Grigoriadis’ ironically expressed conclusion, which is that a multidisciplinary approach is imperative for effective investigation and management of the uncertainties of Fabry disease.
We have obtained written consent to publish the personal medical information contained in this letter from the relevant patients.
Biegstraaten M, Arngr.msson R, Barbey F, et al. Recommendations for initiation and cessation of enzyme replacement therapy in patients with Fabry disease: the European Fabry Working Group consensus document. Orphanet J Rare Dis 2015;10:36.
We are delighted that our paper on exercise-based CR has generated a lively debate(1). We are also pleased that correspondents all agree that our findings are robust(2-4). No correspondents have identified any important RCTs we have overlooked that might have changed our conclusions, and none have challenged the veracity of our findings. The majority of concerns were already addressed in the discussion of our original review, and are clarified below.
Correspondents have identified three main areas for discussion-
1. Mortality as the main metric of effectiveness-
Reduction in all-cause mortality has been the focus of the majority of research in this area. Nineteen of the 22 studies in our review reported on this outcome. It was also the primary outcome in all three previous Cochrane reviews(5-7). This focus on all-cause mortality, or cardiovascular mortality, as the justification for offering exercise-based CR is also reflected in current guidance, and must therefore continue to be of some importance. We provide here some examples-
• NICE Myocardial Infarction secondary prevention; ‘All patients (regardless of their age) should be given advice about and offered a cardiac rehabilitation programme with an exercise component.’ The evidence statements underpinning this recommendation include; ‘Cardiac rehabilitation in patients after MI reduces all-cause and cardiovascular mortality rates provided it includes an exercise component’(8).
• British Heart Foundation; ‘Research shows that cardiac rehab reduces the risk of dying from coronary heart disease…’(9).
• International Council of Cardiovascular Prevention and Rehabilitation; ‘Cardiac rehabilitation (CR) is an established model of care proven to reduce mortality…’(10).
Based on our meta-analysis and the feedback from correspondents, CR programmes, as currently delivered, no longer influence mortality. We are aware that some of the above guidance is outdated and anticipate updated versions will reflect the evidence provided in this paper.
We agree that the outcomes measured in our review should not be the only means of measuring effectiveness. Indeed, at no point do we assert that it should; rather, we explicitly state that exercise-based CR may affect other outcomes, not specifically addressed in our review, such as ‘cardiorespiratory fitness, lifestyle risk factor management, adherence to medication, diet, smoking cessation, psychosocial health and return to work’(1). We believe these are captured in what Professor Buckley and colleagues’ refer to as ‘helping people live better lives whilst managing a major chronic disease’(3). Further, we suggest this should be the focus of future research.
We agree that it is important to consider the potential for CR programmes to improve quality of life, an outcome again discussed in our paper. This has not, however, been a focus of existing research. The available data on quality of life are not suitable for meta-analysis. We can say no more on this than the authors of the 2016 Cochrane review who indicated that nine of our 22 included studies reported a higher quality of life in at least one or more of the subscales measured(6). These data are not sufficient to support the hypothesis that exercise-based CR adds life to years. If exercise-based CR has a meaningful positive effect on quality of life in those with coronary heart disease, similar to that seen in patients with heart failure(11), then we enthusiastically support its use.
2. The most appropriate population and/or interventions have not been compared-
Correspondents question the inclusion of certain studies in our review, with reference to both the population tested and the interventions delivered. Of the 22 studies included in our review, 21 were included in the latest Cochrane review, of which eight studies included patients with angina pectoris and six studies included interventions that were ‘exercise-only’(6). The inclusion of these studies was not disputed when included in the Cochrane review despite providing evidence for the same population.
Correspondents also comment on the review being too focused on exercise. On numerous occasions, our correspondents refer to the influence of exercise-based CR on cardiorespiratory fitness and exercise capacity(2-4). Whilst we agree that exercise is only one part of a complex multi-component intervention, it still remains a key component, especially given evidence linking exercise capacity/cardiorespiratory fitness with longevity(12, 13).
When looking at the nature of the interventions delivered, intervention fidelity, and the extent to which participants adhere to exercise prescription and physical activity guidance, there are substantial weaknesses in the existing literature. We explicitly cite this as the single most important limitation of the CR literature and have detailed this in our review by commenting on ‘dose-response relationship’, ‘under dosage of exercise’, ‘failing to report on the intensity, modality and/or duration of the exercise interventions’ and the lack of ‘reporting of adherence to, and fidelity of, exercise interventions’(1). Adherence/compliance to CR exercise training was recently found to be the most important predictor of outcome(14). However, the overall effect size for all-cause mortality in our review was zero. If risk of death is reduced in those who adhered well to the intervention, there must be an equal sized increase in death rate in those who did not adhere so well. Exactly the same argument applies to considering differential effects related to participants’ baseline characteristics or nature of the interventions. However, we think it is more likely that in the patient groups studied, the interventions tested had no effect, rather than reducing mortality in those who adhered well to the intervention and increasing mortality in the remainder.
3. Old evidence for new programmes in developing countries-
We share our correspondents’ concern about the impact of the global epidemic of cardiovascular disease. Many aspects of the ICCPR’s consensus statement are low cost and have good evidence of effectiveness in high income countries(10). Until such time as suitable evidence is available to support the use of exercise-based CR, this is perhaps where efforts should be focussed.
It is worth reflecting on the reasons why our review has arrived at different conclusions to the previous Cochrane review(6), as cited by Grace et al(2). Neither review concluded that there was a benefit on all-cause mortality. Anderson et al. found an effect on cardiovascular mortality which we did not find(6). In addition to excluding older studies, in contrast to Anderson et al., we calculated the risk difference for death rather than the relative risk for death. To calculate a relative risk, some events are needed. This means that Anderson et al. excluded seven trials from their analysis of all-cause mortality and five from their analysis of cardiovascular mortality because there were no deaths. Excluding trials with no deaths in either arm will, inevitably, overestimate the true effect size. Using our approach makes the maximum use of all recent available data. We think this gives a robust estimate of effectiveness. If there were a beneficial effect on cardiovascular mortality, there would be an interesting debate surrounding the relevance of this, when there is no effect on all-cause mortality.
The continued delivery of exercise-based CR should be supported by contemporary evidence. We are very happy to work with colleagues to develop trials to establish whether CR programmes can be optimised to provide a meaningful improvement in health-related quality of life in high income countries and/or reduce mortality in low income countries.
1. Powell R, McGregor G, Ennis S, Kimani PK, Underwood M. Is exercise-based cardiac rehabilitation effective? A systematic review and meta-analysis to re-examine the evidence. BMJ Open. 2018;8(3):e019656.
2. Grace S. Cardiac Rehabilitation Effectiveness? A response from the Canadian Association of Cardiovascular Prevention and Rehabilitation (CACPR).2018. Available from: http://bmjopen.bmj.com/content/8/3/e019656.responses.
3. Buckley J, Contractor A, Ghisi G, Yeung C, Grace S, L. Cardiac Rehabilitation Effectiveness? *A commentary from the International Council of Cardiovascular Prevention and Rehabilitation.2018. Available from: http://bmjopen.bmj.com/content/8/3/e019656.responses.
4. Cowie A, Murray S, Hinton S, Dalal HM, Nichols S, Taylor R, et al. Response from the British Association for Cardiovascular Prevention and Rehabilitation (BACPR) in collaboration with NACR, the Cochrane Heart Rehabilitation Review Coordination Centre and ACPICR.2018. Available from: http://bmjopen.bmj.com/content/8/3/e019656.responses.
5. Heran BS, Chen JM, Ebrahim S, Moxham T, Oldridge N, Rees K, et al. Exercise-based cardiac rehabilitation for coronary heart disease. Cochrane Database Syst Rev. 2011(7):CD001800.
6. Anderson L, Oldridge N, Thompson DR, Zwisler AD, Rees K, Martin N, et al. Exercise-Based Cardiac Rehabilitation for Coronary Heart Disease: Cochrane Systematic Review and Meta-Analysis. J Am Coll Cardiol. 2016;67(1):1-12.
7. Jolliffe JA, Rees K, Taylor RS, Thompson D, Oldridge N, Ebrahim S. Exercise-based rehabilitation for coronary heart disease. Cochrane Database Syst Rev. 2001(1):CD001800.
8. NICE. MI- secondary prevention- Secondary prevention in primary and secondary care for patients following a myocardial infarction.2013. Available from: https://www.nice.org.uk/guidance/cg172/evidence/myocardial-infarction-se....
9. British Heart Foundation. Cardiac Rehabilitation. 2016. Available from: https://www.bhf.org.uk/publications/heart-conditions/cardiac-rehabilitation.
10. Grace SL, Turk-Adawi KI, Contractor A, Atrey A, Campbell NR, Derman W, et al. Cardiac Rehabilitation Delivery Model for Low-Resource Settings: An International Council of Cardiovascular Prevention and Rehabilitation Consensus Statement. Prog Cardiovasc Dis. 2016;59(3):303-22.
11. Taylor RS, Sagar VA, Davies EJ, Briscoe S, Coats AJ, Dalal H, et al. Exercise-based rehabilitation for heart failure. Cochrane Database Syst Rev. 2014(4):CD003331.
12. Almodhy M, Ingle L, Sandercock GR. Effects of exercise-based cardiac rehabilitation on cardiorespiratory fitness: A meta-analysis of UK studies. Int J Cardiol. 2016;221:644-51.
13. Myers J, Prakash M, Froelicher V, Do D, Partington S, Atwood JE. Exercise capacity and mortality among men referred for exercise testing. N Engl J Med. 2002;346(11):793-801.
14. Abell B, Glasziou P, Hoffmann T. The Contribution of Individual Exercise Training Components to Clinical Outcomes in Randomised Controlled Trials of Cardiac Rehabilitation: A Systematic Review and Meta-regression. Sports Med Open. 2017;3(1):19.
Thank you for the comments from Jessica Price and colleagues. In response to the three points they raised:
For pragmatic and scientific reasons this study did not have a control group as defined by a study group in whom no additional lipid was added/replaced in the diet. Interpretation of a comparison with such a control group would have been challenging in a free-living intervention that did not control the participants’ total energy intake which would have been substantially lower in the control group (by approximately 450 kcal/day based on 9 kcal per gram of fat in the intervention arms). However, we did include a highly relevant comparison group in the trial, taking extra virgin olive oil, as from the existing literature extra virgin olive oil is reported either to have no effect or to lower LDL-cholesterol, so we could also compare coconut oil with olive oil. The pre-specified primary outcome was a comparison of the effect of different fats/oils on changes in LDL-cholesterol. As can be seen in the results, coconut oil was not different from olive oil in terms of the changes in LDL-cholesterol. In addition, we also presented the absolute change in LDL-cholesterol concentrations following the interventions and the groups on coconut oil or olive oil showed no increase in LDL-cholesterol from baseline, if anything a non significant small decrease.
As we state in the report, participants were free to consume the oil any w...
As we state in the report, participants were free to consume the oil any way that they wished. In this trial, the oils/fats were largely consumed as supplements, spreads or mixed into foods as dressings or smoothies without cooking, with occasional stir fry use or incorporation in recipes, but not in repeated high temperature frying. We are aware of the emerging literature on the potential effects of heating on different oils, but the citation provided by Price and colleagues does not provide evidence for the statement they make about “negative impacts on blood lipids and metabolic profiles, increasing LDL-C levels, inflammatory markers and blood pressure”. Indeed, the focus of that review is on repeatedly heated deep-frying oils, and the vast majority of studies included are from animal models and the review did not provide direct evidence for effects on the listed cardiovascular risk markers. As such, their concern is speculative.
Finally, on their last point about the short duration of our study, we agree. Indeed. we raised this as a prime limitation of our work, calling for longer term research and for caution in any translation of this current research into dietary recommendations, which should never be on the basis on any single study but weigh up the body of the evidence. We hope our work will stimulate further research and dialogue on the “need for further elucidation of the more nuanced relationships between different dietary fats and health” as we stated in our article.
Kay-Tee Khaw and Nita Forouhi on behalf of co authors