We thank the authors of the letter in response to our paper for their interest and positive appraisal of our model. Likewise, we appreciate the design of the Multicenter Italian Lung Detection (MILD) trial which, despite its small sample size, demonstrates that annual intervals are unnecessary for the majority of screenees. Once more European data is available to perform cost-effectiveness analyses, we hypothesize that personalised screening intervals will prove to be the preferred design. Furthermore, it is estimated that most inclusion criteria used to select high-risk participants encompass only 70% of all lung cancer cases in the population; reassessing risk and tailoring interval groups after the baseline scan may enable the inclusion of persons of lower risk. As Silva et al mentioned, there is no reason to set the upper limit of follow-up intervals at 2-years. We also agree that volumetric nodule measurements are better suited for determining follow-up procedures than (perpendicular) diameter, and hope to be able to implement this into a future model. Moreover, risk scores may be calculated autonomously by computers in the future, with only a select few dubious cases requiring radiologist attention.
The EPICC trial addresses the rarely investigated topic of rehabilitation in the critical care setting [1]. We note with interest that no improvement was found in outcomes in the rehabilitation group compared to the standard treatment group. Some of the reasons are clearly highlighted by Schaller et al. in their response to the paper including the time to starting intervention, therapy times and also sample size. Only 41% of the participants in the intervention group and 35% of the standard treatment group contributed data throughout the study period. In addition to this, only 8% of the intervention group managed over half the target therapy time and the EPICC trial showed that ‘an extra 10 minutes of physical therapy per day does not make a difference [2]’
This study triggered an audit within our own 16 bedded mixed surgical and medical intensive care department assessing the number of sessions carried out over a 2 week period compared to those attempted. We investigated the actual duration of sessions achieved as compared to a target of 45 minutes rehabilitation each day during the working week (Monday-Friday). On average, 23.3 (standard deviation 20.19 minutes) minutes of rehabilitation per day was achieved and only 35% of attempted physical therapy sessions were completed. These figures are similar to those cited within the EPICC trial and highlight some of the difficulties of achieving longer therapy times within a busy intensive care department. Some of the fac...
The EPICC trial addresses the rarely investigated topic of rehabilitation in the critical care setting [1]. We note with interest that no improvement was found in outcomes in the rehabilitation group compared to the standard treatment group. Some of the reasons are clearly highlighted by Schaller et al. in their response to the paper including the time to starting intervention, therapy times and also sample size. Only 41% of the participants in the intervention group and 35% of the standard treatment group contributed data throughout the study period. In addition to this, only 8% of the intervention group managed over half the target therapy time and the EPICC trial showed that ‘an extra 10 minutes of physical therapy per day does not make a difference [2]’
This study triggered an audit within our own 16 bedded mixed surgical and medical intensive care department assessing the number of sessions carried out over a 2 week period compared to those attempted. We investigated the actual duration of sessions achieved as compared to a target of 45 minutes rehabilitation each day during the working week (Monday-Friday). On average, 23.3 (standard deviation 20.19 minutes) minutes of rehabilitation per day was achieved and only 35% of attempted physical therapy sessions were completed. These figures are similar to those cited within the EPICC trial and highlight some of the difficulties of achieving longer therapy times within a busy intensive care department. Some of the factors cited by our physiotherapists include patient fatigue, limitations on staff availability and also clinical appropriateness of the patients for rehabilitation. Of interest, Schaller et al. have also suggested some solutions to the problems encountered in our own audit and also within the EPICC trial. We agree that the combined effort of the multi-disciplinary team is extremely important in order to maximise opportunities for rehabilitation sessions but also the ability to then consider multiple short sessions each day.
In summary, we applaud the attempts of Wright and colleagues for addressing this under-investigated area of rehabilitation. We have reservations about some of the conclusions of the paper due to limited differences between intervention and treatment and underpowering of the study. Our own unpublished data supports the finding that to consistently achieve 90 minutes of therapy per patient as stipulated for the intervention group in this study would be very difficult in the current framework but this is an area to improve with some solutions already suggested.
References:
1. Wright SE, Thomas K, Watson G, et al. Intensive versus standard physical rehabilitation therapy in the critically ill (EPICC): a multicentre, parallel-group, randomised controlled trial. Thorax 2017:thoraxjnl-2016-209858
2. Schaller SJ, Nydahl P, Blobner M, et al. What does the EPICC trial really tell us? Thorax 2018
In 2011, the National Lung Cancer Screening Trial (NLST) showed that annual low-dose computed tomography (LDCT) improved overall survival (1). More recently, longer interval between LDCT rounds was advocated to improve screening efficiency after baseline (2).
Schreuder et al reported a comprehensive model for optimization of LDCT by biennial rounds for subjects at lower 2-year risk of lung cancer (3). They built a promising polynomial model including both patient characteristics and nodule descriptors. The retrospective simulation on NLST data provided enough power to test Schreuder’s model (3) as well as other models for selection of subjects to be forwarded to biennial screening (2, 4). We appreciate this approach to parsimonious LDCT administration as we are strongly convinced that annual screening should be tailored to subjects with remarkably high risk of lung cancer. The authors refer that prospective randomized controlled trial with tailored screening intervals would be hardly feasible, however we would like to remind that some experience was already reported in the literature.
Since 2005, the Multicenter Italian Lung Detection (MILD) trial conducted a prospective comparison between annual (LDCT1 = 1,152 screenees) and biennial LDCT (LDCT2 = 1,151 screenees) (5). The LDCT2 screenees were shifted to annual screening in case of solid nodule > 60 mm^3 and/or subsolid nodules. In other words, the MILD trial prospectively tested a risk model for tailored s...
In 2011, the National Lung Cancer Screening Trial (NLST) showed that annual low-dose computed tomography (LDCT) improved overall survival (1). More recently, longer interval between LDCT rounds was advocated to improve screening efficiency after baseline (2).
Schreuder et al reported a comprehensive model for optimization of LDCT by biennial rounds for subjects at lower 2-year risk of lung cancer (3). They built a promising polynomial model including both patient characteristics and nodule descriptors. The retrospective simulation on NLST data provided enough power to test Schreuder’s model (3) as well as other models for selection of subjects to be forwarded to biennial screening (2, 4). We appreciate this approach to parsimonious LDCT administration as we are strongly convinced that annual screening should be tailored to subjects with remarkably high risk of lung cancer. The authors refer that prospective randomized controlled trial with tailored screening intervals would be hardly feasible, however we would like to remind that some experience was already reported in the literature.
Since 2005, the Multicenter Italian Lung Detection (MILD) trial conducted a prospective comparison between annual (LDCT1 = 1,152 screenees) and biennial LDCT (LDCT2 = 1,151 screenees) (5). The LDCT2 screenees were shifted to annual screening in case of solid nodule > 60 mm^3 and/or subsolid nodules. In other words, the MILD trial prospectively tested a risk model for tailored screening intervals that was based on baseline LDCT findings. Given the small sample of this trial, we underline that the absence of outcome difference between LDCT1 and LDCT2 should be carefully interpreted (5).
In summary, baseline LDCT2 prospectively selected 147/1,151 (12.8%) screenees for annual screening, whilst 1,004/1,151 (87.2%) were forwarded to biennial round (6). The LDCT2 risk model allowed a sharp reduction by almost 90% LDCTs at the first incidence round. This is a considerable proportion compared to the retrospective analysis presented by Schreuder et al (simulations led to potential LDCT reduction ranging from 10.4% to 81.6%) (3). A similar figure was seen every other year throughout 7.3 years, with overall cuts of 32% LDCTs in LDCT2 compared with LDCT1 (6).
We would like to emphasize that the volumetric risk model allowed higher detection rate in LDCT2 screenees selected for annual screening (1.36% namely 2 lung cancers in 147 screenees) compared to LDCT1 screenees (0.45% namely 5 lung cancers in 1,111 screenees), at the first annual LDCT after baseline. Under this prospective condition, the number of scans needed to diagnose one lung cancer case (NND) was 74 in LDCT2, which is quite close to the 60 NND proposed by Schreuder by accepting a delay of diagnosis in 25% of screenees. On the other hand, NND was 222.2 in LDCT1, namely within the NND range reported in the literature (from 125 to 385) at the first annual LDCT by fixed annual screening algorithms (1, 7, 8). Hence, the LDCT2 algorithm prompted the lowest prospective NND reported in the literature. Through the median 7.3 years of LDCT screening in MILD, the cumulative NND during annual screenings was 63 for selected LDCT2 screenees and 250 for LDCT1 (p=0.003). Selective 3-year screening interval is now being tested in the bioMILD trial with higher volumetric threshold for solid nodules and including circulating biomarkers (ClinicalTrials.gov: NCT02247453; >4,000 baseline LDCTs acquired, results expected by 2020).
We hypothesize that the prospective application of Schreuder’s model might even improve the efficiency of MILD LDCT2. Furthermore, enrichment by clinical variables is encouraged, including circulating biomarkers. More models like Schreuder’s are fostered for optimization of radiologists’ workload for the seemingly approaching practice of population-based lung cancer screening by LDCT.
References
1. National Lung Screening Trial Research T, Aberle DR, Adams AM, Berg CD, Black WC, Clapp JD, et al. Reduced lung-cancer mortality with low-dose computed tomographic screening. The New England journal of medicine. 2011;365(5):395-409.
2. Patz EF, Jr., Greco E, Gatsonis C, Pinsky P, Kramer BS, Aberle DR. Lung cancer incidence and mortality in National Lung Screening Trial participants who underwent low-dose CT prevalence screening: a retrospective cohort analysis of a randomised, multicentre, diagnostic screening trial. The Lancet Oncology. 2016;17(5):590-9.
3. Schreuder A, Schaefer-Prokop CM, Scholten ET, Jacobs C, Prokop M, van Ginneken B. Lung cancer risk to personalise annual and biennial follow-up computed tomography screening. Thorax. 2018.
4. White CS, Dharaiya E, Campbell E, Boroczky L. The Vancouver Lung Cancer Risk Prediction Model: Assessment by Using a Subset of the National Lung Screening Trial Cohort. Radiology. 2017;283(1):264-72.
5. Pastorino U, Rossi M, Rosato V, Marchiano A, Sverzellati N, Morosi C, et al. Annual or biennial CT screening versus observation in heavy smokers: 5-year results of the MILD trial. European journal of cancer prevention : the official journal of the European Cancer Prevention Organisation. 2012;21(3):308-15.
6. Sverzellati N, Silva M, Calareso G, Galeone C, Marchiano A, Sestini S, et al. Low-dose computed tomography for lung cancer screening: comparison of performance between annual and biennial screen. European radiology. 2016;26(11):3821-9.
7. Yousaf-Khan U, van der Aalst C, de Jong PA, Heuvelmans M, Scholten E, Walter J, et al. Risk stratification based on screening history: the NELSON lung cancer screening study. Thorax. 2017.
8. Tammemagi MC, Schmidt H, Martel S, McWilliams A, Goffin JR, Johnston MR, et al. Participant selection for lung cancer screening by risk modelling (the Pan-Canadian Early Detection of Lung Cancer [PanCan] study): a single-arm, prospective study. The Lancet Oncology. 2017.
We are grateful to Dr. Duerden and Dr. Levy for their comments on our paper which highlight the difficulty of comparing doses of ICS steroids when there is no gold standard comparator. Our aim in compiling Table 1 was to point out that the NICE table does not allow for the greater potency of HFA FP compared to HFA BDP. We were concerned that this was a significant safety issue especially in children [1]. In our efforts to simplify this message, we had not fully explained or allowed for some of the other variables.
1. Dr. Levy is correct to point out that the original GINA table (used by NICE) of “Low, medium and high daily doses of inhaled corticosteroid for children 6-11 years” has a statement below indicating that the table is not a table of “dose equivalency”, the term we used in Table 1, but of “estimated clinical comparability”.
2. The GINA table (but not NICE) also has a footnote explaining the inclusion of beclometasone dipropionate CFC (BDP CFC) as a comparison with older literature. CFCs (chlorofluorocarbons), as propellants in metered dose inhalers, were phased out under the Montreal Protocol and were replaced by HFAs (hydrofluorolakanes). However, CFC BDP is still often used as the reference standard when comparing ICS in terms of their potency.
3. Most newer HFA ICSs have been formulated to be equipotent with the CFC ICS they were replacing. As one example, the BTS/SIGN table includes the proprietary HFA BPD, Clenil modulite, commonly us...
We are grateful to Dr. Duerden and Dr. Levy for their comments on our paper which highlight the difficulty of comparing doses of ICS steroids when there is no gold standard comparator. Our aim in compiling Table 1 was to point out that the NICE table does not allow for the greater potency of HFA FP compared to HFA BDP. We were concerned that this was a significant safety issue especially in children [1]. In our efforts to simplify this message, we had not fully explained or allowed for some of the other variables.
1. Dr. Levy is correct to point out that the original GINA table (used by NICE) of “Low, medium and high daily doses of inhaled corticosteroid for children 6-11 years” has a statement below indicating that the table is not a table of “dose equivalency”, the term we used in Table 1, but of “estimated clinical comparability”.
2. The GINA table (but not NICE) also has a footnote explaining the inclusion of beclometasone dipropionate CFC (BDP CFC) as a comparison with older literature. CFCs (chlorofluorocarbons), as propellants in metered dose inhalers, were phased out under the Montreal Protocol and were replaced by HFAs (hydrofluorolakanes). However, CFC BDP is still often used as the reference standard when comparing ICS in terms of their potency.
3. Most newer HFA ICSs have been formulated to be equipotent with the CFC ICS they were replacing. As one example, the BTS/SIGN table includes the proprietary HFA BPD, Clenil modulite, commonly used in children. Clenil is clinically comparable to the legacy BDP CFC with a recommended starting dose of Clenil 50 2 puffs BD (100ug bd) in children (2). The BTS/SIGN table also includes the HFA BDP, Qvar, which is formulated as an extra-fine particle preparation and is usually considered as effective at half the dose. GINA and NICE give the doses for HFA BDP in children as half those of the BDP CFC but do not specify which preparations of HFA BDP they are referring to in their table.
4. HFA Fluticasone propionate (HFA FP) is as effective as other inhaled steroids at approximately half the microgram daily dose (3). So, for clinical comparability HFA FP should be used at half the dose of HFA BDP, as indicated in the BTS/SIGN table.
5. A further complication is that GINA provides doses as daily doses: BTS/SIGN provides puffs and frequency; NICE only specifies dose (though assumed to be daily dose as the table was taken from GINA). In preparing the table we should have made clear that the doses from the BTS/SIGN table were to be given twice a day.
The challenge was how to explain this simply in limited text and a small table and it was complicated by the other points discussed above. To clarify these issues, we suggest the table should be modified as follows:
More fundamentally, this discussion highlights the potential complexity for prescribers from the increasing number of corticosteroid molecules available in an ever-increasing number of devices. If a national guideline body and ‘experts’ who have spent some hours poring over these data struggle to achieve clarity what hope is there for the busy prescriber in clinical practice? Perhaps, this discussion should stimulate regulatory authorities to consider whether manufacturers of inhaled corticosteroids could be required to label their devices as providing doses equivalent to an agreed standard.
Finally, prescribers should always remember that the numbers in all these tables are only a guide. The correct dose of an inhaled steroid is the lowest dose that keeps the patient free of symptoms and that this dose should be adjusted dynamically in response to changes in status in accordance with an agreed action plan.
References
1. Paton J, Jardine E, McNeill E, et al. Adrenal responses to low dose synthetic ACTH (Synacthen) in children receiving high dose inhaled fluticasone. Arch Dis Child. 2006 Oct;91(10):808-13.
2. The electronic Medicines Compendium. https://www. medicines. org. uk/ emc/ medicine/30651 (accessed 14 Jan 2018).
3. The electronic Medicines Compendium. https://www. medicines. org. uk/ emc/ medicine/2913 (accessed 14 Jan 2018).
We welcome the letter by Anna Humphreys and colleagues highlighting the secondary benefits of screening contacts of extra pulmonary tuberculosis for LTBI in areas where active cases are predominantly amongst the non-UK born (1).
We share the view that novel approaches are needed to identify and offer testing to those at risk of LTBI, and that contact tracing provides a unique opportunity to reach those who may be eligible.
Early results from the London Borough of Newham, the pilot site for the national latent TB screening programme highlight that uptake of LTBI screening amongst recent migrants is only 40 percent (2). Efforts are being made to improve awareness including animated health promotion tools (https://youtu.be/tKwAHJ7JeV0) and TB Alert’s Latent TB Handbook (https://www.tbalert.org/health-professionals/ltbi-toolkit/) and novel interventions to improve LTBI screening and treatment uptake are being implemented across the country. We are currently investigating the efficacy of managing LTBI entirely within primary care (https://clinicaltrials.gov/ct2/show/NCT03069807). Recent work has also identified that opportunistic LTBI screening in non-health settings is acceptable to recent migrants (3).
In areas where the majority of active cases are amongst those...
We welcome the letter by Anna Humphreys and colleagues highlighting the secondary benefits of screening contacts of extra pulmonary tuberculosis for LTBI in areas where active cases are predominantly amongst the non-UK born (1).
We share the view that novel approaches are needed to identify and offer testing to those at risk of LTBI, and that contact tracing provides a unique opportunity to reach those who may be eligible.
Early results from the London Borough of Newham, the pilot site for the national latent TB screening programme highlight that uptake of LTBI screening amongst recent migrants is only 40 percent (2). Efforts are being made to improve awareness including animated health promotion tools (https://youtu.be/tKwAHJ7JeV0) and TB Alert’s Latent TB Handbook (https://www.tbalert.org/health-professionals/ltbi-toolkit/) and novel interventions to improve LTBI screening and treatment uptake are being implemented across the country. We are currently investigating the efficacy of managing LTBI entirely within primary care (https://clinicaltrials.gov/ct2/show/NCT03069807). Recent work has also identified that opportunistic LTBI screening in non-health settings is acceptable to recent migrants (3).
In areas where the majority of active cases are amongst those born in high TB-burden countries, a reinterpretation of contact screening that encompasses the aims of identifying active TB cases, as well as recently and remotely acquired LTBI would allow TB programmes to reach many more people at risk.
The National guidelines were updated based on evidence that non-pulmonary TB is a lower risk for transmission (4). Screening contacts is justified given the public health risk of active disease in those recently exposed and a case can be made for screening contacts of extra pulmonary cases as they may have been infected by a previously unknown pulmonary index case.
However, should we decide to change our approach to screening contacts with the explicit aim of identifying LTBI due to remote infection then we must at least acknowledge this when we talk to patients about their recent contacts and ask them to share personal information. And, as a TB community, we must agree that this approach is ethical.
We would support this broader eligibility for screening contacts and believe it would strengthen an already vital tool in the fight to eliminate Tuberculosis in the UK.
1. Humphreys A, Abbara A, Williams S, John L, Corrah T, McGregor A, et al. Screening contacts of patients with extrapulmonary TB for latent TB infection. Thorax. 2018;73(3):277-8.
2. Loutet M. National Roll-out of Latent Tuberculosis Testing and Treatment for New Migrants in England: a retrospective evaluation in a high-incidence area. European Respiratory Journal. 2017:1-25.
3. Walker CL, Duffield K, Kaur H, Dedicoat M, Gajraj R. Acceptability of latent tuberculosis testing of migrants in a college environment in England. Public Health. 2018;158:55-60.
4. Hoppe LE, Kettle R, Eisenhut M, Abubakar I. Tuberculosis—diagnosis, management, prevention, and control: summary of updated NICE guidance. BMJ. 2016:h6747-9.
We have read with great interest the multi-centred EPICC trial that randomized over 300 patients [1]. While the delivery of a complex physical rehabilitation intervention in clinical trials is difficult, we believe that several aspects of the trial may have resulted in the inability to detect a difference between the control and intervention groups. These factors include the delayed time to start the intervention, inadequate delivery of the intervention and the large loss to follow-up for the primary outcome measure. In our opinion, these three factors limit the interpretation of the results of the study. While the authors have mentioned some of these concerns in their discussion, and Connolly et al. raised some of these points already [2], we hope to learn some important lessons from the authors to better understand these limitations and how they can be minimized in future studies.
The number of randomized controlled trials evaluating early physical rehabilitation in ICUs is increasing [3]. Positive effects on primary outcomes were only found in studies in which physical rehabilitation was started within 72 hours of ICU admission [4-6]. Studies, which did not meet this criterion of early onset of physical rehabilitation, did not demonstrate benefit of the intervention [7]. Therefore, this time frame has been defined in rehabilitation guidelines [8]. Based on this evidence, we are not surprised that the authors of the EPICC trial were unable to demonstrate beneficial...
We have read with great interest the multi-centred EPICC trial that randomized over 300 patients [1]. While the delivery of a complex physical rehabilitation intervention in clinical trials is difficult, we believe that several aspects of the trial may have resulted in the inability to detect a difference between the control and intervention groups. These factors include the delayed time to start the intervention, inadequate delivery of the intervention and the large loss to follow-up for the primary outcome measure. In our opinion, these three factors limit the interpretation of the results of the study. While the authors have mentioned some of these concerns in their discussion, and Connolly et al. raised some of these points already [2], we hope to learn some important lessons from the authors to better understand these limitations and how they can be minimized in future studies.
The number of randomized controlled trials evaluating early physical rehabilitation in ICUs is increasing [3]. Positive effects on primary outcomes were only found in studies in which physical rehabilitation was started within 72 hours of ICU admission [4-6]. Studies, which did not meet this criterion of early onset of physical rehabilitation, did not demonstrate benefit of the intervention [7]. Therefore, this time frame has been defined in rehabilitation guidelines [8]. Based on this evidence, we are not surprised that the authors of the EPICC trial were unable to demonstrate beneficial effects of their intervention, since it approximately started on day 8 (the median (IQR) duration of ventilation at randomisation was 4 (3–7) days with a further 3 (1–6) days until the first physical rehabilitation was received), which may be too late to confer benefit.
The EPICC protocol aimed to compare 30 min vs. 90 min of physical rehabilitation, which was not achieved in either group. The authors report that the daily physical therapy was applied for 23 min in the intervention group (26% of the planned intervention) and for 13 min in standard of care group (43% of the planned standard care), respectively. Not only this amount of physical rehabilitation is hardly conceivable as an effective therapeutic strategy, but in terms of testing the hypothesis, it did not achieve the planned separation between the groups. In other words, the EPICC trial teaches us that an additional 10 minutes of physical rehabilitation per day does not make a difference.
The authors describe two main reasons for not achieving their planned intervention: (a) sedation and (b) patient fatigue. We have difficulties understanding why these two factors could not be controlled. The authors do not report the sedation regime during the study. If there was no standardized sedation protocol with daily awakening trials, this is a further shortcoming of the protocol as well as another reason for inability to improve the patients’ outcome in the intervention group. Deep sedation not only inhibits effective physical rehabilitation but is associated with increased mortality and length of stay [8]. To better appreciate the study results, it would be important that the authors report the sedation protocols/regimes of the participating centres.
Furthermore, how was the treatment plan of the intervention in “difficult” patients with low physical reserve or pre-existing frailty implemented? From our own experience patients with impaired functional reserves or frailty might only be trained for a short period of time. However, to achieve an intervention time of 90 minutes per day, such patients must be trained several times a day (e.g. for 15 minutes every hour). If 23 minutes are achieved in the intervention group, there might have been an additional “resource” limitations which is not presented, e.g. that a physical therapist would not be able to do more than a session every 4 hours or than four times a day. Would it be possible to elaborate on the available staff resources to deliver the intervention? If we assume that the lack of staff resources were an additional limitation not mentioned by the authors, it supports our belief that a successful early rehabilitation program has to be interprofessional, including both physical therapists and nursing staff to maximize physical rehabilitation opportunities throughout the day [5, 10].
Finally, the authors chose a primary outcome (Physical Component Summary Score of the SF-36 version 2) that does take into account mortality. Approximately one third of patients enrolled died before the functional outcome could be assessed. This functional outcome “truncated due to death” creates challenges in the definition and statistical evaluation of the treatment effect, and deserves careful planning of statistical analyses [11].
An additional 25% of enrolled patients were lost to follow-up. Therefore 57% of the enrolled patients did not contribute to the primary outcome measure, making the overall results of the study difficult to interpret.
In summary, we think that the conclusion and key message do not entirely reflect the study results. Physical therapy interventions of 90 min vs. 30 minutes were not achieved in the study. Additionally, less than half of enrolled patients contributed data to the primary outcome measure and excluding patients who did not survive limits the interpretation of this complex intervention.
References
1. Wright, S.E., et al., Intensive versus standard physical rehabilitation therapy in the critically ill (EPICC): a multicentre, parallel-group, randomised controlled trial. Thorax, 2017.
2. Connolly B and Denehy L Hindsight and moving the needle forwards on rehabilitation trial design. Thorax. 2018 Mar;73(3):203-205. doi: 10.1136/thoraxjnl-2017-210588. Epub 2017 Nov 14. http://thorax.bmj.com/content/73/3/203
3. Fuest, K. and S.J. Schaller, Recent evidence on early mobilization in critical-Ill patients. Curr Opin Anaesthesiol, 2018.
4. Schweickert, W.D., et al., Early physical and occupational therapy in mechanically ventilated, critically ill patients: a randomised controlled trial. Lancet, 2009. 373(9678): p. 1874-82.
5. Schaller, S.J., et al., Early, goal-directed mobilisation in the surgical intensive care unit: a randomised controlled trial. Lancet, 2016. 388(10052): p. 1377-1388.
6. Investigators, T.S., et al., Early mobilization and recovery in mechanically ventilated patients in the ICU: a bi-national, multi-centre, prospective cohort study. Crit Care, 2015. 19: p. 81.
7. Moss, M., et al., A Randomized Trial of an Intensive Physical Therapy Program for Patients with Acute Respiratory Failure. Am J Respir Crit Care Med, 2016. 193(10): p. 1101-10.
8. Bein, T., et al., S2e guideline: positioning and early mobilisation in prophylaxis or therapy of pulmonary disorders : Revision 2015: S2e guideline of the German Society of Anaesthesiology and Intensive Care Medicine (DGAI). Anaesthesist, 2015. 64 Suppl 1: p. 1-26.
9. Stephens, R.J., et al., Practice Patterns and Outcomes Associated With Early Sedation Depth in Mechanically Ventilated Patients: A Systematic Review and Meta-Analysis. Crit Care Med, 2018. 46(3): p. 471-479.
10. McWilliams, D., et al., Earlier and enhanced rehabilitation of mechanically ventilated patients in critical care: A feasibility randomised controlled trial. J Crit Care, 2018. 44: p. 407-412.
11. Colantuoni, E., et al., Statistical methods to compare functional outcomes in randomized controlled trials with high mortality. BMJ, 2018. 360: p. j5748.
The article of Bhatt et al addresses an important topic (1). The authors assessed the relative contribution of intensity and duration of tobacco smoke exposure to the development of chronic obstructive pulmonary disease (COPD). They concluded that smoking duration alone provides stronger risk than the composite index of pack years. In other words, the effect of long and low intensity exposure has a stronger association with COPD than short exposures of high intensities. The article of Marks consents this finding, concluding that pack years are a suboptimal index of exposure (2).
A major limitation of the study of Bhatt, which surprisingly is not stated as such, is the use of a cross-sectional design that does not allow drawing causal conclusions. The conclusions drawn therefore might be flawed.
Selection bias due the healthy ‘survivor’ effect might have occurred. The duration of smoking could have been influenced by the deleterious effects a person experiences from the exposure to smoke. Those with a long smoke duration are more likely not to experience (or experience less) health issues due to smoking, and might therefore have less severe (or no) COPD than those with a short smoke duration. In line with this, selective ‘drop-out’ of the more diseased persons may have biased the results.
Furthermore, the authors use retrospective data, while this often leads to recall bias. Participants often do not precisely remember the numbers of cigarettes smoked...
The article of Bhatt et al addresses an important topic (1). The authors assessed the relative contribution of intensity and duration of tobacco smoke exposure to the development of chronic obstructive pulmonary disease (COPD). They concluded that smoking duration alone provides stronger risk than the composite index of pack years. In other words, the effect of long and low intensity exposure has a stronger association with COPD than short exposures of high intensities. The article of Marks consents this finding, concluding that pack years are a suboptimal index of exposure (2).
A major limitation of the study of Bhatt, which surprisingly is not stated as such, is the use of a cross-sectional design that does not allow drawing causal conclusions. The conclusions drawn therefore might be flawed.
Selection bias due the healthy ‘survivor’ effect might have occurred. The duration of smoking could have been influenced by the deleterious effects a person experiences from the exposure to smoke. Those with a long smoke duration are more likely not to experience (or experience less) health issues due to smoking, and might therefore have less severe (or no) COPD than those with a short smoke duration. In line with this, selective ‘drop-out’ of the more diseased persons may have biased the results.
Furthermore, the authors use retrospective data, while this often leads to recall bias. Participants often do not precisely remember the numbers of cigarettes smoked per day in a specific year or time period. Assuming that participants underestimate smoke intensity, it is likely that the association between smoke intensity and COPD is less strong than the association between smoke duration and COPD. This weaker association is then not due to the relative contribution of smoke intensity compared to that of duration, but to recall bias.
To conclude, the statements made in the paper seem to be very convincing, but are based on research with methodological limitations. Prospective studies assessing the relative contribution of smoke intensity and smoke duration are thus urgently needed.
1. Bhatt SP, Kim YI, Harrington KF, Hokanson JE, Lutz SM, Cho MH, et al. Smoking duration alone provides stronger risk estimates of chronic obstructive pulmonary disease than pack-years. Thorax. 2018.
2. Marks GB. Guiding policy to reduce the burden of COPD: the role of epidemiological research. Thorax. 2018.
We read with interest the latest BTS guideline for the management of non-tuberculous mycobacterial pulmonary disease (NTM-PD).1
Of particular interest was the section relating to the treatment of Mycobacterium abscessus –pulmonary disease. The evidence for the treatment regimes remains poor (Grade D) and within paediatric population the experience of treatment strategies is based on both adult guidelines and clinical expertise. Questions remain about the rationale for the use of macrolides in organisms with inducible resistance. Table 8 in the article recommends the use of oral macrolides during both induction and continuation phase even if inducible macrolide resistance has been demonstrated in vitro. By definition, M. abscessus abscessus strains will possess a functional erm(41) gene, 2 and therefore we feel use of this drug may be inappropriate for this subspecies.
Azithromycin is a bacteriostatic antibiotic, with intracellular penetration superior to that of the aminoglycosides. 3 M. abscessus complex can thrive within the intracellular environment. 4 Given the exposure of intracellular M. abscessus abscessus to a bacteriostatic agent we suggest this may induce not only resistance but also quiescence within the bacterium and therefore the bactericidal action of aminoglycosides would be significantly impaired given the lack of active protein synthesis. This quiescent state is likely given the difficulty in isolating this organism whilst the...
We read with interest the latest BTS guideline for the management of non-tuberculous mycobacterial pulmonary disease (NTM-PD).1
Of particular interest was the section relating to the treatment of Mycobacterium abscessus –pulmonary disease. The evidence for the treatment regimes remains poor (Grade D) and within paediatric population the experience of treatment strategies is based on both adult guidelines and clinical expertise. Questions remain about the rationale for the use of macrolides in organisms with inducible resistance. Table 8 in the article recommends the use of oral macrolides during both induction and continuation phase even if inducible macrolide resistance has been demonstrated in vitro. By definition, M. abscessus abscessus strains will possess a functional erm(41) gene, 2 and therefore we feel use of this drug may be inappropriate for this subspecies.
Azithromycin is a bacteriostatic antibiotic, with intracellular penetration superior to that of the aminoglycosides. 3 M. abscessus complex can thrive within the intracellular environment. 4 Given the exposure of intracellular M. abscessus abscessus to a bacteriostatic agent we suggest this may induce not only resistance but also quiescence within the bacterium and therefore the bactericidal action of aminoglycosides would be significantly impaired given the lack of active protein synthesis. This quiescent state is likely given the difficulty in isolating this organism whilst the patient is exposed to macrolides and explains the recommendation of discontinuing long term macrolide use prior to resampling for M. abscessus abscessus. Furthermore, the use of macrolides for the treatment of other Mycobacterial species (for example M. fortuitum or M. smegmatis) that possess functional erm genes is not recommended. 5 Thus when declaring someone to have cleared M. abscessus when on treatment, can one really be sure that this is not simply an assumption of quiescent state to later rear its’ ugly head? Likewise the declaration of a re-emergence on cessation of treatment may be the head rearing.
Much of the experience of macrolide use appears historical dating back to the mid 1990s, and their apparent efficacy reflects pre-subspeciating taxonomy where strains may have been identified as M. abscessus but in actual fact could have been M. abscessus massiliense with dysfunctional erm(41) genes and therefore macrolide sensitivity. 2
Although we welcome a guideline to direct clinical practice, we note that there has been little progress in updating the evidence and this most recent guideline is based on treatment protocols devised almost 25 years ago which do not reflect advances in bacterial taxonomy and genetic analysis of antimicrobial resistance. Work to delineate optimal therapy for M. abscessus complex infections is urgently warranted.
Ref.
1. Haworth et al. (2017). Thorax 72: Suppl 2
2. Bastian et al. (2011). Anti Agen & Chemo 55: 775-781
3. Carryn et al. (2003). Infect. Dis. Clin. N. Am 17: 615-634
4. Medjahed et al. (2010). Trend Micro 18: 117-123
5. Nagh et al. (2005). JAC 55: 170-177
While I agree this paper draws out most of the important issues related to the NICE guideline, I would like to point out that there are inaccuracies regarding the statements and table related to 'dose equivalences' in the GINA document.
In fact reference to equivalence in your article is explicitly contradicted by the statement immediately below GINA table 3-6, which states that 'this is not a table of equivalence, but of estimated clinical comparability'. (1)
Furthermore the GINA table also takes into account the potential for side-effects. For example, BDP HFA causes more adrenal suppression than FP HFA at the same dose. (2)
Of course this is going to get even more complicated with the number of generics now available, as they cannot be assumed to be equivalent to the original product, due to the impact of the inhaler device and additives.
(1) www.ginasthma.org
(2) Fowler, S. J., Orr, L. C., Wilson, A. M., Sims, E. J. and Lipworth, B. J. (2001), Dose-response for adrenal suppression with hydrofluoroalkane formulations of fluticasone propionate and beclomethasone dipropionate. British Journal of Clinical Pharmacology, 52: 93-95. doi:10.1046/j.0306-5251.2001.bjcp.1399.x
We thank Associate Professor Magnus Ekström et al for their research letter regarding our Cochrane Review: Opioids for the palliation of refractory breathlessness in adults with advanced disease and terminal illness (1,2). We also acknowledge that following the publication of their letter in Thorax, feedback was provided through the appropriate mechanism to the Cochrane Review Group (2). We have published a detailed response to their comments in the feedback section of our review, however, given the seriousness of the criticisms published in Thorax, we think it is important that our response also sit alongside their Thorax letter.
We acknowledge the statistical difficulties in the interpretation and summation of the complex data on opioids for breathlessness. One such issue is the inclusion of crossover studies in a meta-analysis, however, a crossover design is an appropriate way to assess short term interventions, particularly when patient recruitment may be challenging. The Cochrane Handbook outlines several methods to incorporate crossover data into meta-analyses (3). In using the data as if it was a parallel study, the limitations should be acknowledged, in that it can give rise to a unit of analysis error whereby confidence intervals may be wide, and the overall effect is under-estimated. An alternative method is to calculate correlation co-efficients (which describe the ratio of between-patient standard deviation with the within patient variation) to impute...
We thank Associate Professor Magnus Ekström et al for their research letter regarding our Cochrane Review: Opioids for the palliation of refractory breathlessness in adults with advanced disease and terminal illness (1,2). We also acknowledge that following the publication of their letter in Thorax, feedback was provided through the appropriate mechanism to the Cochrane Review Group (2). We have published a detailed response to their comments in the feedback section of our review, however, given the seriousness of the criticisms published in Thorax, we think it is important that our response also sit alongside their Thorax letter.
We acknowledge the statistical difficulties in the interpretation and summation of the complex data on opioids for breathlessness. One such issue is the inclusion of crossover studies in a meta-analysis, however, a crossover design is an appropriate way to assess short term interventions, particularly when patient recruitment may be challenging. The Cochrane Handbook outlines several methods to incorporate crossover data into meta-analyses (3). In using the data as if it was a parallel study, the limitations should be acknowledged, in that it can give rise to a unit of analysis error whereby confidence intervals may be wide, and the overall effect is under-estimated. An alternative method is to calculate correlation co-efficients (which describe the ratio of between-patient standard deviation with the within patient variation) to impute a corrected standard error. Some included studies provided appropriate data to calculate this (standard error of the differences), or a corrected standard error can be imputed using “borrowed” correlation co-efficients from other studies.
In our Cochrane Review we used the former method (2). In response to the feedback provided by Ekström et al, we conducted a sensitivity analysis with an alternative meta-analysis (accounting for use of cross over data) using correlation co-efficients and corrected standard errors. The data are presented using standardised mean differences. The results demonstrate a change from baseline SMD -0.14 (95% CI -0.40 to 0.13) and a post treatment score SMD -0.55 (95% CI -0.76 to -0.35) (Figure 1, https://doi.org/10.6084/m9.figshare.5743137). This is similar to our original published results which found a change from baseline score SMD -0.09 (95% CI -0.36 to 0.19) and a post treatment score SMD -0.28 (95% CI -0.5 to -0.05). Both analyses draw the same conclusion that there is a significant but small effect size for the use of opioids for breathlessness.
Ekström et al raise concerns regarding the use of a fixed effects versus a random effects model (1). Based on the assumption that studies would have a small sample size we chose a priori to use a fixed effects model. As Higgins and Green describe: a random effects model will award relatively more weight to smaller studies because smaller studies are more informative for learning about the distribution of the effects across studies than for learning about an assumed common intervention effect (3). Therefore, if a random effects model is inappropriately applied, in particular, if the results of small studies are systematically different to the results of larger ones, the random effects model can inappropriately exacerbate the effects of any bias (4).
The choice and rationale for a fixed effects model was outlined in advance in our protocol. This protocol was peer reviewed prior to publication (2). Consistent with Higgins and Green, we presented both a fixed effects and random effects model in the sensitivity analysis, and found no differences in effect (3). Following additional sensitivity analysis as described above, there remains very little difference between the fixed effects model in the change from baseline scores (SMD -0.14 (95% CI -0.40 to 0.13)) and the random effects model (SMD -0.21 (95% CI -0.55 to 0.12)), and in the post treatment score fixed effects model (SMD -0.55 (95% CI -0.76 to -0.35)) and random effects model (SMD -0.69 (95% CI -1.08 to -0.29)).
A second limitation from the opioids for breathlessness data is the use of different scales to measure the same outcome (e.g. visual analogue scale (VAS) or Borg scale), with scales measured on different lengths, with different extremes, and different gradations of intensity. In order to combine data on different scales, standardised mean differences are required, which are calculated by dividing the mean difference by a pooled estimate of the between-patient standard deviation. However, combining this between-patient standard deviation with the within patient variation imputed from the corrected standard error described as above to incorporate crossover trials is not always possible from the available data. It is difficult to interpret the resulting standardised mean differences from cross-over trials.
Transforming the data as described above works if the data are reported as either change from baseline or post treatment scores, however it is unclear if it is also appropriate to combine them in a single meta-analysis, and to combine them in a single meta-analysis using standardised mean difference (SMD). Higgins and Green state that post treatment scores can be combined with change from baseline scores when using an unstandardised mean difference, however, they should not be combined as a standardised mean difference using the standard deviation of the change scores (as these are not the same units as the standard deviation of the final scores) (3). Therefore, it makes it difficult to combine data from different scales as outlined above, as well as combining post treatment and change from baseline scores in one single meta-analysis. Originally, we separated post treatment and change from baseline scores. In a further subsequent sensitivity analyses performed in response to the feedback, we combined these but separated by scale, see Figure 2 (https://doi.org/10.6084/m9.figshare.5743134.v2).
Ekström et al discussed at length the primary outcome of breathlessness, but they did not take into account adverse events or multidimensional assessment of the use of opioids (1). We noted increased adverse events including drowsiness, nausea, and constipation, as well as a significant difference in the mastery domain scores in one included trial, suggesting that participants may feel less in control when using morphine. We believe it is important to consider the evidence in its entirety, rather than focusing on only one effect size score.
Ekström et al have suggested that we downgraded the quality of evidence based on concerns about study size alone (1). We used GRADE methodology to rate the quality of the evidence and our decision to downgrade the quality of the evidence was based on the fact that more than 50% of included trials did not report on allocation concealment, blinding of participants or personnel, or blinding of outcome assessment. This is potentially a serious limitation when the primary outcome (i.e. change in breathlessness) is entirely subjective. We acknowledge that study size per se does not influence the internal validity of trial results and that some of the trials included in the review were designed with sufficient statistical power.
The ‘size bias’ criterion was suggested by the Cochrane editorial team during the review process of our manuscript, as there is empiric evidence that study size may be a surrogate marker of trial quality when the reporting on aspects of trial quality is poor (4). In other fields, small study effects have been shown to distort the results of meta-analyses (5). Many of the papers included in the review did not provide sufficient information to adequately assess trial quality, and because all the studies included were small in relative terms (with less than 50 participants per trial) we believe that it is important to highlight that the quantitative data synthesis was based on the pooling of relatively small studies.
We included the study by Woodcock 1982, but this is more correctly referenced in our review as Bar-Or 1982 (6). We included the study by Johnson et al (2002) in the review, but excluded it from the meta-analyses as the data was not normally distributed and medians and interquartile ranges cannot be imputed into a meta-analysis, consistent with the Cochrane Handbook (3, 7). Although Ekström et al commented that study selection should align to predefined eligibility criteria with reasons for exclusion stated to minimise selection bias, our studies were selected according to a published protocol with study types, inclusion and exclusion criteria specified (1).
While we value the opinion provided by Ekström et al, the additional sensitivity analyses reported here do not change our review conclusions (1,2). There is some small, low quality evidence that shows benefit for the use of parental or oral opioids to palliate breathlessness in the short term. The magnitude of this benefit is at best modest and given the potential adverse events and the lack of any evidence suggesting an improvement in overall quality of life, longer-term studies with multi-dimensional scales are required to ascertain whether any benefits outweigh the potential long-term risks, particularly where opioids are being used in those with chronic stable disease in the outpatient setting (8).
Acknowledgements
We thank Christopher Cates for his extensive input on this sensitivity analysis and comments on this letter, Kerry Dwan, Toby Lasserson and the Statistical Methods Group, and Julian Higgins for his report on the interpretation of this data.
References:
1. Ekström M, Bajwah S, Bland JM, Currow D, Hussain J, Johnson M. One evidence base; three stories: do opioids relieve chronic breathlessness? Thorax 2017
2. Barnes H, McDonald J, Smallwood N, Manser R. Opioids for the palliation of refractory breathlessness in adults with advanced disease and terminal illness. Cochrane Database of Systematic Reviews 2016, Issue 3. Art. No.: CD011008. DOI: 10.1002/14651858.CD011008.pub2.
3. Higgins JPT, Green S (editors). Cochrane Handbook for Systematic Reviews of Interventions Version 5.1.0 [updated March 2011]. The Cochrane Collaboration, 2011. Available from www.cochrane-handbook.org.
4. Kjaergard LL, Villumsen J, Gluud C. Reported methodologic quality and discrepancies between large and small randomized trials in meta-analyses. Annals of Internal Medicine 2001;135(11):982-9.
5. Nüesch E, Trelle S, Reichenbach S, Rutjes AW, Tschannen B, Altman DG, et al. Small study effects in meta-analyses of osteoarthritis trials: meta-epidemiological study. BMJ 2010;341:c3515.
6. Bar-Or D, Marx JA, Good J. Breathlessness, alcohol and opiates. The New England Journal of Medicine 1982;306(22):1363–4.
7. Johnson MJ, McDonagh TA, Harkness A, McKayd SE, Dargie HJ. Morphine for the relief of breathlessness in patients with chronic heart failure--a pilot study. European Journal of Heart Failure 2002;4(6):753–6.
Figure 1: https://doi.org/10.6084/m9.figshare.5743137 Meta-analysis – Opioids for palliation of breathlessness conducted using alternative methods for use of crossover data with results separated according to post treatment scores and change from baseline scores.
Figure 2: https://doi.org/10.6084/m9.figshare.5743134.v2 Meta-analysis – Opioids for the palliation of breathlessness using alternative method for use of crossover data, combining post treatment and change from baseline scores but separating by scale used to measure breathlessness.
We thank the authors of the letter in response to our paper for their interest and positive appraisal of our model. Likewise, we appreciate the design of the Multicenter Italian Lung Detection (MILD) trial which, despite its small sample size, demonstrates that annual intervals are unnecessary for the majority of screenees. Once more European data is available to perform cost-effectiveness analyses, we hypothesize that personalised screening intervals will prove to be the preferred design. Furthermore, it is estimated that most inclusion criteria used to select high-risk participants encompass only 70% of all lung cancer cases in the population; reassessing risk and tailoring interval groups after the baseline scan may enable the inclusion of persons of lower risk. As Silva et al mentioned, there is no reason to set the upper limit of follow-up intervals at 2-years. We also agree that volumetric nodule measurements are better suited for determining follow-up procedures than (perpendicular) diameter, and hope to be able to implement this into a future model. Moreover, risk scores may be calculated autonomously by computers in the future, with only a select few dubious cases requiring radiologist attention.
The EPICC trial addresses the rarely investigated topic of rehabilitation in the critical care setting [1]. We note with interest that no improvement was found in outcomes in the rehabilitation group compared to the standard treatment group. Some of the reasons are clearly highlighted by Schaller et al. in their response to the paper including the time to starting intervention, therapy times and also sample size. Only 41% of the participants in the intervention group and 35% of the standard treatment group contributed data throughout the study period. In addition to this, only 8% of the intervention group managed over half the target therapy time and the EPICC trial showed that ‘an extra 10 minutes of physical therapy per day does not make a difference [2]’
Show MoreThis study triggered an audit within our own 16 bedded mixed surgical and medical intensive care department assessing the number of sessions carried out over a 2 week period compared to those attempted. We investigated the actual duration of sessions achieved as compared to a target of 45 minutes rehabilitation each day during the working week (Monday-Friday). On average, 23.3 (standard deviation 20.19 minutes) minutes of rehabilitation per day was achieved and only 35% of attempted physical therapy sessions were completed. These figures are similar to those cited within the EPICC trial and highlight some of the difficulties of achieving longer therapy times within a busy intensive care department. Some of the fac...
In 2011, the National Lung Cancer Screening Trial (NLST) showed that annual low-dose computed tomography (LDCT) improved overall survival (1). More recently, longer interval between LDCT rounds was advocated to improve screening efficiency after baseline (2).
Show MoreSchreuder et al reported a comprehensive model for optimization of LDCT by biennial rounds for subjects at lower 2-year risk of lung cancer (3). They built a promising polynomial model including both patient characteristics and nodule descriptors. The retrospective simulation on NLST data provided enough power to test Schreuder’s model (3) as well as other models for selection of subjects to be forwarded to biennial screening (2, 4). We appreciate this approach to parsimonious LDCT administration as we are strongly convinced that annual screening should be tailored to subjects with remarkably high risk of lung cancer. The authors refer that prospective randomized controlled trial with tailored screening intervals would be hardly feasible, however we would like to remind that some experience was already reported in the literature.
Since 2005, the Multicenter Italian Lung Detection (MILD) trial conducted a prospective comparison between annual (LDCT1 = 1,152 screenees) and biennial LDCT (LDCT2 = 1,151 screenees) (5). The LDCT2 screenees were shifted to annual screening in case of solid nodule > 60 mm^3 and/or subsolid nodules. In other words, the MILD trial prospectively tested a risk model for tailored s...
We are grateful to Dr. Duerden and Dr. Levy for their comments on our paper which highlight the difficulty of comparing doses of ICS steroids when there is no gold standard comparator. Our aim in compiling Table 1 was to point out that the NICE table does not allow for the greater potency of HFA FP compared to HFA BDP. We were concerned that this was a significant safety issue especially in children [1]. In our efforts to simplify this message, we had not fully explained or allowed for some of the other variables.
1. Dr. Levy is correct to point out that the original GINA table (used by NICE) of “Low, medium and high daily doses of inhaled corticosteroid for children 6-11 years” has a statement below indicating that the table is not a table of “dose equivalency”, the term we used in Table 1, but of “estimated clinical comparability”.
2. The GINA table (but not NICE) also has a footnote explaining the inclusion of beclometasone dipropionate CFC (BDP CFC) as a comparison with older literature. CFCs (chlorofluorocarbons), as propellants in metered dose inhalers, were phased out under the Montreal Protocol and were replaced by HFAs (hydrofluorolakanes). However, CFC BDP is still often used as the reference standard when comparing ICS in terms of their potency.
3. Most newer HFA ICSs have been formulated to be equipotent with the CFC ICS they were replacing. As one example, the BTS/SIGN table includes the proprietary HFA BPD, Clenil modulite, commonly us...
Show MoreWe welcome the letter by Anna Humphreys and colleagues highlighting the secondary benefits of screening contacts of extra pulmonary tuberculosis for LTBI in areas where active cases are predominantly amongst the non-UK born (1).
We share the view that novel approaches are needed to identify and offer testing to those at risk of LTBI, and that contact tracing provides a unique opportunity to reach those who may be eligible.
Early results from the London Borough of Newham, the pilot site for the national latent TB screening programme highlight that uptake of LTBI screening amongst recent migrants is only 40 percent (2). Efforts are being made to improve awareness including animated health promotion tools (https://youtu.be/tKwAHJ7JeV0) and TB Alert’s Latent TB Handbook (https://www.tbalert.org/health-professionals/ltbi-toolkit/) and novel interventions to improve LTBI screening and treatment uptake are being implemented across the country. We are currently investigating the efficacy of managing LTBI entirely within primary care (https://clinicaltrials.gov/ct2/show/NCT03069807). Recent work has also identified that opportunistic LTBI screening in non-health settings is acceptable to recent migrants (3).
Show MoreIn areas where the majority of active cases are amongst those...
We have read with great interest the multi-centred EPICC trial that randomized over 300 patients [1]. While the delivery of a complex physical rehabilitation intervention in clinical trials is difficult, we believe that several aspects of the trial may have resulted in the inability to detect a difference between the control and intervention groups. These factors include the delayed time to start the intervention, inadequate delivery of the intervention and the large loss to follow-up for the primary outcome measure. In our opinion, these three factors limit the interpretation of the results of the study. While the authors have mentioned some of these concerns in their discussion, and Connolly et al. raised some of these points already [2], we hope to learn some important lessons from the authors to better understand these limitations and how they can be minimized in future studies.
Show MoreThe number of randomized controlled trials evaluating early physical rehabilitation in ICUs is increasing [3]. Positive effects on primary outcomes were only found in studies in which physical rehabilitation was started within 72 hours of ICU admission [4-6]. Studies, which did not meet this criterion of early onset of physical rehabilitation, did not demonstrate benefit of the intervention [7]. Therefore, this time frame has been defined in rehabilitation guidelines [8]. Based on this evidence, we are not surprised that the authors of the EPICC trial were unable to demonstrate beneficial...
The article of Bhatt et al addresses an important topic (1). The authors assessed the relative contribution of intensity and duration of tobacco smoke exposure to the development of chronic obstructive pulmonary disease (COPD). They concluded that smoking duration alone provides stronger risk than the composite index of pack years. In other words, the effect of long and low intensity exposure has a stronger association with COPD than short exposures of high intensities. The article of Marks consents this finding, concluding that pack years are a suboptimal index of exposure (2).
A major limitation of the study of Bhatt, which surprisingly is not stated as such, is the use of a cross-sectional design that does not allow drawing causal conclusions. The conclusions drawn therefore might be flawed.
Selection bias due the healthy ‘survivor’ effect might have occurred. The duration of smoking could have been influenced by the deleterious effects a person experiences from the exposure to smoke. Those with a long smoke duration are more likely not to experience (or experience less) health issues due to smoking, and might therefore have less severe (or no) COPD than those with a short smoke duration. In line with this, selective ‘drop-out’ of the more diseased persons may have biased the results.
Furthermore, the authors use retrospective data, while this often leads to recall bias. Participants often do not precisely remember the numbers of cigarettes smoked...
Show MoreSir
We read with interest the latest BTS guideline for the management of non-tuberculous mycobacterial pulmonary disease (NTM-PD).1
Of particular interest was the section relating to the treatment of Mycobacterium abscessus –pulmonary disease. The evidence for the treatment regimes remains poor (Grade D) and within paediatric population the experience of treatment strategies is based on both adult guidelines and clinical expertise. Questions remain about the rationale for the use of macrolides in organisms with inducible resistance. Table 8 in the article recommends the use of oral macrolides during both induction and continuation phase even if inducible macrolide resistance has been demonstrated in vitro. By definition, M. abscessus abscessus strains will possess a functional erm(41) gene, 2 and therefore we feel use of this drug may be inappropriate for this subspecies.
Azithromycin is a bacteriostatic antibiotic, with intracellular penetration superior to that of the aminoglycosides. 3 M. abscessus complex can thrive within the intracellular environment. 4 Given the exposure of intracellular M. abscessus abscessus to a bacteriostatic agent we suggest this may induce not only resistance but also quiescence within the bacterium and therefore the bactericidal action of aminoglycosides would be significantly impaired given the lack of active protein synthesis. This quiescent state is likely given the difficulty in isolating this organism whilst the...
Show MoreWhile I agree this paper draws out most of the important issues related to the NICE guideline, I would like to point out that there are inaccuracies regarding the statements and table related to 'dose equivalences' in the GINA document.
In fact reference to equivalence in your article is explicitly contradicted by the statement immediately below GINA table 3-6, which states that 'this is not a table of equivalence, but of estimated clinical comparability'. (1)
Furthermore the GINA table also takes into account the potential for side-effects. For example, BDP HFA causes more adrenal suppression than FP HFA at the same dose. (2)
Of course this is going to get even more complicated with the number of generics now available, as they cannot be assumed to be equivalent to the original product, due to the impact of the inhaler device and additives.
(1) www.ginasthma.org
(2) Fowler, S. J., Orr, L. C., Wilson, A. M., Sims, E. J. and Lipworth, B. J. (2001), Dose-response for adrenal suppression with hydrofluoroalkane formulations of fluticasone propionate and beclomethasone dipropionate. British Journal of Clinical Pharmacology, 52: 93-95. doi:10.1046/j.0306-5251.2001.bjcp.1399.x
We thank Associate Professor Magnus Ekström et al for their research letter regarding our Cochrane Review: Opioids for the palliation of refractory breathlessness in adults with advanced disease and terminal illness (1,2). We also acknowledge that following the publication of their letter in Thorax, feedback was provided through the appropriate mechanism to the Cochrane Review Group (2). We have published a detailed response to their comments in the feedback section of our review, however, given the seriousness of the criticisms published in Thorax, we think it is important that our response also sit alongside their Thorax letter.
We acknowledge the statistical difficulties in the interpretation and summation of the complex data on opioids for breathlessness. One such issue is the inclusion of crossover studies in a meta-analysis, however, a crossover design is an appropriate way to assess short term interventions, particularly when patient recruitment may be challenging. The Cochrane Handbook outlines several methods to incorporate crossover data into meta-analyses (3). In using the data as if it was a parallel study, the limitations should be acknowledged, in that it can give rise to a unit of analysis error whereby confidence intervals may be wide, and the overall effect is under-estimated. An alternative method is to calculate correlation co-efficients (which describe the ratio of between-patient standard deviation with the within patient variation) to impute...
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