eLetters

665 e-Letters

  • Response to comment by Prof. Hughes

    Dr Hughes raises an important point that we also address in discussing limitations of the study. We did not take meta-analyses into consideration that had combined studies with inactive treatments and treatment as usual (TAU) as control interventions. We based this decision primarily on methodological reasons. TAU varies widely across patients and settings and can include antidepressant or behavioral treatments. Therefore, equating TAU with placebo treatment or waiting list seemed problematic for us.

    Nevertheless, Dr. Hughes’ point is well taken. TAU is an important reference standard, particularly in pragmatic studies because it reflects real-world conditions. In a meta-analysis, however, TAU is difficult to handle especially when the components of TAU across individual trials are not well documented. Using TAU in a meta-analysis often comes down to combining apples and oranges without being able to tell which treatments are the apples and which are the oranges.

    Dr. Hughes also argues that patients on waiting lists cannot be prevented from getting some form of treatment. We agree but view this as a general issue of contamination that is almost impossible to control, particularly in pragmatic studies. The fact that, in our study, patients on active treatments had substantially larger treatment effects than those on waiting lists makes us think that contamination issues probably did not have much impact.

  • Response to Dr Conviser's comments

    Dear Dr Conviser,

    Thank you for your comments. Please find our responses to those comments below, itemised 1 to 6:

    1. Your protocol calls for 8 months of exposure to the bio Density system. Manufacturers recommendations supported by peer reviewed studies have shown that BMD changes require a minimum of 9 months and many individuals begin to show changes with DEXA at the 11 and 12 month period.

    OUR RESPONSE:
    Could you please clarify to which specific manufacturer recommendations and peer-reviewed studies you refer?
    We note that BMD changes have indeed been observed within 6 months when an intervention has been sufficiently intense [1]. A single BMU will complete a full remodelling cycle in roughly 4 months, but we certainly agree the mineralisation lag limits sensitivity of ionising radiation devices to detect change before 6 months [2]. We therefore balanced an imperative to apply our intervention for longer than 6 months to increase our opportunity to detect a BMD treatment effect, with the requirement to complete the trial within the time period that we have access to the bioDensity device. Our confidence that 8 months will provide a sufficient intervention duration is derived from the BMD response observed in the LIFTMOR trial for women where we applied the identical training duration (see early findings publication [3] - final outcomes are under revision.) In light of your concerns, we are interested in the rationale behind your ch...

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  • Note on grey literature search strategy

    Since publication of the article, we have been made aware that although we had identified and included a number of grey literature reports using the Sheffield Alcohol Policy Model, some reports by the Sheffield team had not been identified by our search strategy. As with many systematic reviews, our efforts searching for studies mainly focused on published peer-reviewed literature. Given the nature of and interest in alcohol minimum unit pricing by a number of think tanks, had we also included the websites of leading think tanks in our search.

    Some of the unidentified reports overlap to varying degrees with peer-reviewed studies by the same team which had been included in our review, such as Purshouse 2010, Holmes 2014 and Meier 2016. However had we identified others (listed below), these would have been included in the article. Whilst they use the same model and are conducted by the same team, they would nevertheless have lent further support for the consistency, specificity, dose-response, plausibility and coherence criteria.

    The conclusions of our article are unaffected, with the evidence suggesting strongly that MUP will reduce alcohol consumption and harm

    Angus, C., Meng, Y., Ally, A., Holmes, J. and Brennan, A. (2014) 'Model-based appraisal of minimum unit pricing for alcohol in Northern Ireland: An adaptation of the Sheffield Alcohol Policy Model version 3', Sheffield: ScHARR, University of Sheffield.
    Angus C, Holmes J,...

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  • Revised standardised mortality ratios for underlying and mentioned cause Parkinson’s Disease

    Since the publication of our mortality study of a workforce manufacturing paraquat [1], the cohort which had been flagged by the Medical Research Information Service of the National Health Service (now NHS Digital) has had to be pseudonymised. This provided an opportunity to check the records held by NHS Digital against our own. We were also able to flag some individuals who it had not been possible to trace when originally sent to be flagged thirty years previously, including one worker known to have died but with unknown cause of death. As a consequence, three new deaths were identified which had occurred before the end of follow up (30 June 2009). Two deaths occurred in workers that we had previously thought were alive at the end of follow up, and one in a worker who could not previously be traced and who had been treated as lost to follow up.

    Most of the reported standardised mortality ratios (SMR) were little changed. However, one of the newly identified deaths was due to Parkinson’s Disease (PD), the primary endpoint, and has increased the number of observed deaths due to PD from one to two versus 1.8 expected (SMR=110; 95% CI 13 to 400). Similarly the number of death certificates mentioning PD has increased from one to two versus 3.3 expected (SMR=61; 95% CI 7 to 222). Nevertheless, the extra death due to PD doesn’t change the conclusion of the paper that there was no evidence of increased mortality (underlying and mentioned cause) from PD. Furthermore none...

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  • Clinical algorithm and sample size

    Dear Sydney-
    I have a number of concerns regarding the design of the SLATE trial that I would like to share. There are two important questions regarding ART initiation in ambulatory patients that you are addressing. The first is how to appropriately screen patients for conditions that preclude immediate initiation of ART and the second is the best time to initiate ART in ambulatory patients.
    The SLATE protocol begins with addressing the first question with a step-wise algorithm to identify patients who require further investigation for a variety of clinical conditions but most notably tuberculosis and cryptococcal disease. The first stage is a standardised WHO TB symptom screen which has been shown to be have an inadequate negative predictive value in high burden settings, particularly in patients who are not on ART. Rangaka et al (Clinical Infectious Diseases 2012;55(12):1698–706) showed in a South African cohort that 8.9% of patients with a negative symptoms screen who were not on ART had culture confirmed TB. More recently Hanifa et al (CROI 2015 abstract number: 823) showed that around 5.6% of patients who were recently diagnosed with HIV had a negative symptom screen but culture confirmed TB. The SLATE algorithm provides for further assessment for TB in patients without symptoms but this relies on a symptom-guided physical exam, this is poorly defined and it is unclear how this will pick-up TB in asymptomatic patients. It is therefore likely that between 5...

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  • A high workload is a heavy workload

    Letter to the Editor

    Topic: A high workload is a heavy workload

    I was quite interested to read that Rippstein-Leuenbergeret al., (2017), made reference to ‘high workload’ as an area that is very stressful for nurses. High workload may be regarded as ‘the ratio of nurses to the number of patients’ (Carayon & Gurses, 2008), and ‘the number of nursing interventions related to direct patient care’ (Lee et al., 2017).
    As a registered nurse with over 20 years of experience working in Emergency rooms in hospitals both in England and the United States, and teaching, I am able to relate to the highly stressful work areas experienced by nurses working not only in Intensive Care Units but also in other areas as well . In my experiences, nurses typically made references to ‘heavy workload’ to also describe high nurse to patient ratios, compared to ‘high workload’ as used by the above authors.
    According to Carlesi et al.,(2017), and Lee et al., (2017), ‘high workload’ and ‘heavy workload’ (Kendall-Raynor, 2011; Hakonsen et al., 2010) are used in studies to refer to the same thing. In fact, Carayon and Gurses (2008) used both terms in their study.
    It is my humble suggestion, therefore, that as both ‘high workload’ and ‘heavy workload’ are terms that can, and have been, used interchangeably to mean the same thing, this letter should be amended to the above study to allay any misconception that may arise from future readership.

    “A qualita...

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  • Why exclude treatment-as-usual?

    This fascinating paper has a serious flaw; the exclusion of all studies with treatment-as-usual (TAU) comparison conditions. The authors justify this decision by stating that TAU is not standardized and cannot be considered an inactive condition. However, the difference between TAU and two included control conditions (wait-list and no care) may be predominantly semantic. Patients randomized to no care or wait-list cannot be forbidden from continuing to participate in the healthcare system and may receive exactly the treatments that they would usually receive if they were not enrolled in a clinical trial; that is, treatment as usual. No care and wait-list may not be any more standardized than TAU. Furthermore, TAU is what happens in the real world. Given the state of the mental health infrastructure in many countries, behavioural treatments are often compared against TAU to see if they are beneficial compared to what the patient would receive otherwise.

  • Unwarranted conclusion may be supported by additional analyses

    I have read the authors’ report on the investigation of data collection mode effects during administration of a three-item patient-reported patient-centered communication measure with interest. While I greatly appreciate the work the authors invested in the study, I think one of their major conclusions is not supported by the reported analyses. It is repeatedly stated throughout the manuscript that the relative clinician performance rankings were stable across the different data collection modes. However, the analytic strategy described in the Methods section, the perfectly identical distances between physicians (on the logit-scale) across modes in Figure 1, and the detailed results made available in the Supplementary Appendices suggest that they included the clinician identifiers as main effects in the analyses without specifying an interaction term between data collection mode and physician identifiers. This means that the ranking of (and even equal metric distance in logit units between) clinicians was restricted to be identical across all levels of the covariates, including administration mode, by the statistical model. In other words, the stable clinician ranking was rather a non-falsifiable assumption than a finding of the analyses.
    This does not mean that the authors’ conclusion is necessarily wrong, only that the performed analyses did not check the hypothesis of constant clinician ranking across modes as intended. Additional analyses may show that this hypot...

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  • Re: Lack of evidence for interventions offered in UK fertility centres

    To The Editor, BMJ

    Dear Dr Godlee

    Balen et al have responded to our papers. [1,2] In our BMJ open paper we systematically identified 276 claims of benefit relating to 41 different fertility interventions and 16 published references were cited 21 times on 13 of the 74 websites we searched.[1] In our BMJ analysis paper, we systematically examined the evidence for ‘38 additional fertility interventions’ and found evidence of improvements in live birth rates for only five interventions. We used standard critical appraisal techniques (as detailed in our paper) to explore the quality of these studies. We identified that for all five of these interventions the studies had methodological problems, raising uncertainty about the significance of the results. This is a serious issue for patients, public health, public trust, and regulators.

    Balen et al suggest that our evidence review included - and found evidence lacking for - things which are not “add-ons”. We classified ‘add-ons’ in the BMJ analysis article in response to peer review where the issue was discussed (see online peer review comments).

    Peer review comment: ‘The methodology has led them to five interventions for which there may be some evidence of improvement in live birth rates. One of these is intrauterine insemination in a natural cycle. This is an alternative treatment, rather than an “add-on”, and usually not one applied to the population who require IVF, and certainly not one intended to...

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  • Occasional drinking increases depression, regular reduces?

    Some of the conclusions here seem to leave out important data. In particular, the conclusion that occasional drinking increases risk of depression is stated, yet there is no discussion of the discordant finding that "regular" drinking appears to significantly decrease the risk of depression. Without plausible explanatory theories, this kind of discordance does not encourage me to place trust in the findings.

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