On 2017 Oct 17, Stuart RAY commented:

A paper Inbar R, 2016 with the same authors and a nearly-identical title was previously published in Vaccine and retracted by the publisher.

On 2016 Aug 16, Niels Vrang commented:

We welcome discussion and critique although we do not approve of the rather broad spectrum of points raised in this comment. We do stand by our results which have been generated by several skilled technicians and scientists known in the art of neuroscience and the methods employed live up to scientific standards. Our findings are but a series of findings trying to understand the putative role of GLP-1 agonists in neurodegenerative disorders and in this particular case the findings were negative. The discussion of the paper clearly recognise that others have found positive data. We believe that the best way to advance science is by reporting both positive and negative data and we are thankful for PLoS One for making the reporting of negative findings possible.

On 2016 Aug 08, Christian Holscher commented:

This is a misleading and unscientific paper. The authors measure amyloid plaque load in a London mutation APP mouse model which does not develop amyloid plaques! In the London mutation, the amyloid stays mostly inside the cells. Fig. 5 clearly shows that the brains are virtually free of plaques, yet the authors conclude that the drug failed to reduce amyloid plaque load! They should have measured total amyloid levels using the western blot technique. The memory tasks are similarly dubious. The wild type control mice are a lot lighter than the transgenic mice (Fig 1A) and they swim a lot faster in the water maze (Fig. 3A-C), which makes the interpretation of the result questionable. The reduced latency can be explained entirely by the faster swim speed. The memory tests of the APP/PS1 mice are just as unscientific. Fig. 4 shows that the saline treated APP/PS1 mice do not show a memory deficit in both tasks when compared to controls. The drug cannot improve a non-existing memory deficit! The experiment did not work and needs to be repeated. Showing these graphs in the publication is misleading. This study is deeply flawed and the conclusions are not supported by the data shown. It should be retracted.

Prof. Christian Holscher, PhD Lancaster University, UK

On 2016 Sep 17, Jonathan Eisen commented:

The first author of this paper wrote a blog post about the work at microBEnet. See http://microbe.net/2016/08/10/green-space-influences-human-health-and-airborne-microbial-communities/

On 2016 Sep 05, David Evans commented:

Mendelian randomization (MR) is an epidemiological method that can be used to strengthen causal inference regarding the relationship between a modifiable environmental exposure and a medically relevant trait and to estimate the magnitude of this relationship [1]. Whilst the principles on which MR are based are relatively easy to comprehend, many scientists report finding it difficult to understand the method at first. Reviews of MR that present the methodology and concrete examples in the context of particular biomedical issues may be of considerable value in introducing the ideas to practitioners and researchers in different fields, and several have appeared [2,3].

In a recent issue of Nature Reviews Rheumatology, Robinson et al. review some of the theory behind MR as well as application of the technique to the field of rheumatology [4]. Whilst a useful introduction for a rheumatology audience, Robinson et al.’s article contains some errors and inaccuracies in the description of the MR method that might mislead researchers who attempt to apply the approach based on this review. There are some infelicities in the description of some biological processes (e.g. the authors’ contend in their abstract that “alleles for genetic variants are randomly inherited at meiosis”- this is false- alleles are inherited at conception, not during meiosis), but here we have restricted ourselves to pointing out some of the issues that are directly relevant to the theory and practice of MR:

(1) The authors seem to be confused in the choice of independent and dependent variables in the two stage least squares instrumental variables regression analyses. The correct way of describing the first stage of this procedure is that the exposure is regressed on the instrumental variable (not vice versa as the authors sometimes do in their manuscript). In addition, the second panel of Figure 2 in their paper illustrates fitted values from the first stage analysis regressed on the outcome variable. This is not correct. The second stage of the two stage least squares procedure is equivalent to regressing the outcome variable on the fitted values from the first stage regression (not vice versa). The authors also do not comment on the requirement of correcting the standard errors of the parameter estimates should the analysis be performed in this two-step fashion (although most statistics packages that implement two stage least squares regression will do this automatically for the user). We also point out that technically the authors describe a variant of a two-stage residual inclusion estimator rather than two-stage least squares [5].

(2) The visual description of residuals in the first panel of Figure 2 is incorrect. As in ordinary least squares regression, residuals refer to the part of the dependent variable (here urate) that is not predicted by the regression. The residuals should therefore be represented by vertical double headed arrows between the individual data points and the regression line, not by horizontal double headed arrows between the data points and the regression line.

(3) The authors claim that “The genotypic measure of exposure is simple to obtain and being objective is not subject to experimental biases (such as recall bias)”. Whilst it is true that genotypes are not subject to many of the biases common in classical epidemiology, they are still subject to possible measurement error (i.e. genotyping error, imputation uncertainty and population stratification), all of which must be borne in mind to ensure that the results of any MR analysis are robust.

(4) The authors mistakenly claim that it is straight forward to demonstrate that a genetic variant is not related to possible confounders of the exposure outcome association. We disagree. Whilst it is usually elementary to show that a genetic variant is associated with an exposure of interest (hence satisfying one of the core assumptions for a valid genetic instrument), demonstrating that a genetic variant is not associated with factors that confound the association between exposure and outcome is impossible [6]. The best an investigator can hope to do is to show that the putative genetic instrument is unrelated to a range of potential confounding variables [7]. If no association is found (or fewer associations than are expected by chance), then this will increase confidence that the genetic variant fulfils this core assumption, but an investigator can never prove this assumption outright since there may still be residual/unmeasured confounders/confounding that are associated with the genetic variants but have not been tested explicitly.

(5) The authors misunderstand the nature of two sample MR analysis and the Wald statistic used in this procedure. The authors claim that the Wald method does not provide an estimate of the causal effect of the exposure on the outcome. This is false. The Wald method provides estimates of the causal effect of the exposure on the outcome and their standard errors [8]. The authors also claim that MR analysis requires measurement of the biological exposure. Again this false. Investigators can use two sample MR on summary results data obviating the requirement of measuring an exposure variable in their analyses, and indeed this is one of the benefits of this type of analysis [9].

(6) The authors misinterpret results obtained from the Durbin Wu Hausman statistic (a statistical test typically used to compare observational and instrumental variable estimates of the association between the exposure and the outcome). They incorrectly state that, in the presence of reverse causality, estimates from an MR analysis will be in the direction opposite to the observational association. This is not the case. In reality, reverse causality would result in a causal estimate of zero rather than an estimate in the opposite direction to the observational association (assuming that the genetic variant that instruments the exposure is a valid instrument). Typically a significant Durbin Wu Hausman statistic indicates a difference between observational and causal estimates of the exposure-outcome association and can be a result of the presence of latent confounding in the observational analysis or indeed reverse causality. The statistic makes the strong assumption that the model for the instrumental variable analysis is valid, and also often has low power.

Finally, we note that the authors have failed to mention several recent extensions of MR methodology that allow relaxation of some aspects of the IV assumptions, providing forms of sensitivity analysis to conventional approaches [10,11]. These will become progressively more useful as the number of genetic variants known to be related to various medically relevant exposures increases. Extensive discussion of the MR methodology as well as some recent developments in sensitivity analyses are available elsewhere [9,12,13].

David M Evans, Tom Palmer, George Davey Smith

References

[1] Davey Smith et al (2003). Int J Epidemiol, 32(1):1-22.

[2] Jansen et al (2014). Eur Heart J, 35(29), 1917-24.

[3] Sekula et al (in press). J Am Soc Nephrol.

[4] Robinson et al (2016). Nat Rev Rheumatol, 12(8), 486-96.

[5] Terza et al (2008). J Health Econ, 27, 531-543.

[6] Didelez et al (2007). Stat Methods Med Res, 16:309-30.

[7] Davey Smith et al (2007). PLOS Med, 4(12), e352.

[8] Pierce et al (2013). Am J Epidemiol, 178:1177–84.

[9] Davey Smith et al (2014). Hum Mol Genet, 23(R1):R89-98.

[10] Bowden et al (2015). Int J Epidemiol, 44(2):512-25.

[11] Bowden et al (2016). Genet Epidemiol, 40(4):304-14.

[12] Evans et al (2015). Ann Rev Genom Hum Genet, 16:327-50.

[13] Burgess et al (in press). Epidemiology.

On 2016 Nov 01, Melissa Rethlefsen commented:

I thank Dr. Thombs for his responses, particularly for pointing out the location of the search strategy in the appendix of Thombs BD, 2014. I am still uncertain whether the search strategies in question were the ones used to validate whether the primary studies would be retrieved ("In addition, for all studies listed in MEDLINE, we checked whether the study would be retrieved using a previously published peer-reviewed search [9].") for two reasons: 1) The cited study (Sampson M, 2011, about the method of validation) does not include the search strategy Dr. Thombs notes below, though the strategy is cited previously when the search to identify meta-analyses meeting the inclusion criteria was discussed, and 2) The search strategy in Thombs BD, 2014 is very specific to the "Patient Health Questionnaire." Was this search strategy modified to include other instruments? Or was the Patient Health Questionnaire the only depression screening tool in this project? It appeared as though other scales were included, such as the Geriatric Depression Scale and the Hospital Anxiety and Depression Scale, hence my confusion.

I greatly appreciate the information about the reduction in the number of citations to examine; this is indeed highly beneficial information. I am curious whether the high number of citations came from primarily the inclusion of one or more Web of Science databases? Looking at the Thombs BD, 2014 appendix, multiple databases (SCI-EXPANDED, SSCI, A&HCI, CPCI-S, CPCI-SSH) were searched in the Web of Science platform. Were one or more of those a big contributor to extra citations retrieved?

Though Dr. Thombs and his colleagues make excellent points about the need to maximize resources at the expense of completeness, which I fully agree with, my concern is that studies which do post-hoc analysis of database contributions to systematic reviews lead those without information retrieval expertise to believe that searching one database is comprehensive, when in fact, the skill of the searcher is the primary factor in recall and precision. Most systematic review teams do not have librarians or information specialists, much less ones with the skill and experience of Dr. Kloda. I appreciate that Dr. Thombs acknowledges the importance of including information specialists or librarians on systematic review teams, and I agree with him that the use of previously published, validated searches is a highly promising method for reducing resource consumption in systematic reviews.

On 2016 Oct 26, Brett D Thombs commented:

We thank Ms. Rethlefson for her comments on our study. We agree with her about the importance of working with a skilled information specialist or librarian on all systematic reviews and that, as she notes, the quality of searches is often very poor in systematic reviews. She has correctly noted some of the limitations in our study, as we did in the study itself. We do not share Ms. Rethlefson’s concern with our use of what she refers to as an “uncited search strategy in an unspecified version of MEDLINE on the Ovid SP platform.” The full peer-reviewed search strategy that we used is provided in the appendix of the systematic review protocol that we cited (1). Ms. Rethlefson seems to criticize this approach because it “can only find 92% of the included articles, versus the 94% available in the database.” Systematic reviews are done for different purposes, and there is always a balance between resource consumption and completeness. In many cases, identifying 94% of all test accuracy evidence will be sufficient, and, in those cases, identifying 92% is not substantively different. Ms. Rethlefson questioned whether searching only MEDLINE would indeed reduce the number of citations and the burden in evaluating them. She is correct that we did not assess that. However, based on our initial search (not including updates) for studies of the diagnostic test accuracy of the Patient Health Questionnaire (1), using MEDLINE only would have cut the total number of citations to process from 6449 to 1389 (22%) compared to searching MEDLINE, PsycINFO, and Web of Science. Thus, it does seem evident, that in this area of research, using such a strategy would have a significant impact on resource use. Whether or not it is the right choice depends on the specific purposes of the systematic review and would be conditional on using a well-designed, peer-reviewed search.

(1) Thombs BD, Benedetti A, Kloda LA, et al. The diagnostic accuracy of the Patient Health Questionnaire-2 (PHQ-2), Patient Health Questionnaire-8 (PHQ-8), and Patient Health Questionnaire-9 (PHQ-9) for detecting major depression: protocol for a systematic review and individual patient data meta-analyses. Systematic Reviews. 2014;3:124.

On 2016 Oct 21, Melissa Rethlefsen commented:

The authors are asking an important question—which database(s) should be searched in a systematic review? Current guidance from the Cochrane Collaboration, the Institute of Medicine, and most information retrieval specialists suggests that searching multiple databases is a necessity for a comprehensive search of the literature, but searching multiple databases can be time-consuming and may result in more citations than are manageable to review. In this paper, the authors posit that searching MEDLINE alone would be sufficient to locate relevant studies when conducting systematic reviews with meta-analysis on depression screening tools.

Though the authors’ methodology is detailed, one limitation noted in the paper was noted as, “we were unable to examine whether the search strategies used by authors in each meta-analysis did, in fact, identify the articles indexed in MEDLINE as most included meta-analyses did not provide reproducible search strategies.” Because of this, the conclusions of this study must be viewed with caution. If the searches conducted by the authors did not locate the studies in MEDLINE, the fact that the studies could have theoretically been located in MEDLINE is irrelevant. Finding results in MEDLINE is largely due to the ability of the searcher, the sensitivity of the search design, and the skill of the indexer.Wieland LS, 2012 Suarez-Almazor ME, 2000 Golder S, 2014 O'Leary N, 2007 Searching for known items to assess database utility in systematic reviews has been previously done (see, for example, Gehanno JF, 2013), but it has been critiqued due to the lack of search strategy assessment.Boeker M, 2013 Giustini D, 2013

The authors, using an uncited search strategy in an unspecified version of MEDLINE on the Ovid SP platform they state had been “a previously published peer-reviewed search,” indeed can only find 92% of the included articles, versus the 94% available in the database. Unfortunately, there is little reason to suppose that the authors of systematic review articles can be expected to conduct a “reasonable, peer-reviewed search strategy.” In fact, researchers have repeatedly shown that even fully reproducible reported search strategies often have fatal errors and major omissions in search terms and controlled vocabulary.Sampson M, 2006 Rethlefsen ML, 2015 Koffel JB, 2016 Golder S, 2008 Though working with a librarian or information specialist is recommended as a way to enhance search strategy quality, studies have shown that certain disciplines never work with librarians on their systematic reviews Koffel JB, 2016, and those disciplines where it is more common still only work with librarians about a third of the time.Rethlefsen ML, 2015 Tools like PRESS were developed to improve search strategies McGowan J, 2016, but search peer review is rarely done. Rethlefsen ML, 2015

The authors also state that, “searching fewer databases in addition to MEDLINE will result in substantively less literature to screen.” This has not been shown by this study. The authors do not report on the number of articles retrieved by their search or any of the searches undertaken in the 16 meta-analyses they evaluate. Furthermore, no data on precision, recall, or number needed to read was given for either their search or for the meta-analyses. These data could be reconstructed and would give readers concrete information to make this case. That would be particularly helpful in light of the information provided about the number and names of the databases searched. Other studies looking at database performance for systematic reviews have included precision and recall information for the original search strategies and/or from the reported found items. Preston L, 2015 Bramer WM, 2013 Bramer WM, 2016 These studies have largely found that searching multiple databases is of benefit.

On 2016 Aug 04, Martine Crasnier-Mednansky commented:

Expression of crp in Escherichia coli was found 'not to be' post-transcriptionally regulated by sRNAs including SdsR (Lee HJ, 2016). In sharp contrast, this paper reports SdsR 'strongly' affects the expression of crp in Salmonella typhimurium. What causes such discrepancy?

In all fairness, Lee HJ, 2016 noted "a few sRNAs [which included SdrS] were close to the two-fold cutoff for repression of crp" and also noted "our translational fusions will only detect regulation in the 5’ UTR and the first 20 codons of the targets". Therefore, it was prudently suggested that expression of crp was not affected by sRNAs.

Here, the authors observed a two-fold repression of crp by SdsR using whole genome microarray (table 1), and an almost 2-fold repression using a gfp reporter fusion (figure 1B). Thus it appears there is no data discrepancy between the present work and Lee HJ, 2016.

The contention by the authors SdsR strongly affects the expression of crp is in relation to data obtained with sRNA CyaR (as reported in figure 6). Figure 6A indicates that, in early stationary phase, there is no synthesis of SdsR. SdsR appears at +3h when the cells are supposedly well advanced in the stationary phase. This suggests regulation by SdsR occurs late in the stationary phase, as mentioned by the authors. Figure 6A also indicates constitutive SdsR is overly expressed, and most importantly the correlation between SdsR and crp mRNA is not straightforward, as observed by comparing lane 4 and 10 (or 11) in figure 6A.

CyaR expression is positively regulated by CRP-cAMP (De Lay N, 2009), therefore a carbon source triggering a relatively high cAMP level as compared to glucose (maltose in this paper), caused an increase in the CyaR level both in the presence and absence of SdsR (figure 6B, lane 1 to 8). With SdsR overly expressed, the CyaR level significantly decreased for cells grown on maltose (figure 6B, lane 11 and 12). The authors concluded lack of CyaR is related to the repression of crp by SdsR yet the level of CRP was not monitored.

It is reasonable to conclude regulation of crp expression by sRNAs does not appear physiologically relevant during growth or entry into stationary phase. However, this regulation may be significant upon accumulation of SdsR in nutrient-limited cells. If this is the case, CRP-dependent synthesis of post-exponential starvation proteins, which are not essential for survival (Schultz JE, 1988), will gradually be shut off. This attempted proposal is grounded in data from Lévi-Meyrueis C, 2014 indicating lack of SdsR results in impaired competitive fitness however only after 2 to 3 days in stationary phase.

On 2017 Mar 05, Antonio Palazón-Bru commented:

None

On 2017 Mar 05, Antonio Palazón-Bru commented:

Dear Dr Martí-Carvajal,

Thank you very much for your interest in our work. In the paper we had written the following phrase about the indicated issue: "ROMPA has a stratified randomisation based on gender, age (≤65 or >65 years) and Simplified Acute Physiology Score (SAPS) III score (<50 or ≥51)." Please, if you have any doubt about this, do not hesitate to contact us for further information.

Best regards, The authors

On 2017 Feb 16, Arturo Martí-Carvajal commented:

This protocol reported an unclear randomization process. 1. How sequence generation was done? 2. How do trial authors assured the ramdoness?

On 2016 Nov 10, Lydia Maniatis commented:

The inexplicable insistence on a logically and empirically invalid elementaristic approach is reflected in Gheorghiu et al’s description of color as a “low-“level feature” (of the proximal, distal, perceptual ? – stimulus): “Together these studies suggest that while symmetry mechanisms are sensitive to across-the-symmetry-midline correlations in low-level features such as color…” I’ve already discussed the problem with describing symmetry (or asymmetry) as a collection of correlations; here, the point has to do with color. Color, as we know, is not a feature of the distal stimulus, or of the proximal stimulus, it is a feature and a product of perceptual processes. As we (visual perception types) know, furthermore, there is no unique collection of wavelengths associated with the perception of a given color. How a local patch will look is wholly dependent on the structure and interpretation (via process) of the surrounding patches as well as that particular one. A patch reflecting the full spectrum of wavelengths in the visible spectrum can appear any color we want, because of the possibility of perceiving transparency and double layers of color. (Google/Image Purves cubes to see an example). So, although the term “low-level” is rather vague, it is clear that the perceived color of a patch in the visual field is the result of the highest level of perceptual processes, up to and including the process that produces consciousness. This type of fundamental confusion at the root of a research program should call that program into question.

On 2016 Nov 08, Lydia Maniatis commented:

Point 3

A persistent question that I have is why is it acceptable, in the world of psychophysics, for authors to act as subjects, especially when the number of observers is typically so small, and when authors are careful to point out that non-author subjects were "naive."

Quoting Gheorghiu et al: "Six observers participated in the experiments: the first author and five subjects who were naive with regard to the experimental aims."

Indeed, in certain conditions, the lead author acted as one of only three, or even of only two, subjects:

"For the number of blobs experiment three observers (EG, RA, CM) took part in all stimulus conditions and for the stimulus presentation duration experiment only two observers (EG and RA) participated."

If naivete is important, then why is this acceptable? It seems like a straightforward question. Maybe there's a straigthforward answer, but I don't know where to find it.

On 2016 Nov 07, Lydia Maniatis commented:

The authors are asking questions of the nature: “How many types of phlogiston does wood contain,” comparing the results of burning wood in a variety of conditions, and interpreting them under the assumptions of “phlogiston detection theory.”

The key point is that their major assumption or hypothesis - the existence of phlogiston, is never questioned or tested even though evidence and arguments against it are of long-standing. Here, ‘phlogiston’ is equivalent to “symmetry channels” and ‘assumptions of ‘phlogiston detection theory’ are equivalent to the assumptions of “probability summation of independent color-symmetry channels within the framework of signal-detection theory.”

As noted in the earlier post, signal detection is a wholly inappropriate concept with respect to perception. But this doesn’t inhibit the study from proceeding, because logical problems are ignored and data is simply interpreted as though the “framework of sdt” were applicable.

The basic logical problem is that the perception of a symmetrical form derives from the detection of local symmetry elements. These local elements supposed to instigate local signals, which are summed, and this sum mediates whether symmetry will or will not be perceived:

“In the random-segregated condition the local symmetry signals would be additively combined into a single color-selective symmetry channel, producing a relatively large symmetry signal in that color channel and zero symmetry signal in the other color channels. In the non-segregated condition on the other hand, there would be symmetry information in all channels but the information in each channel would be much weaker…Probability summation across channels would result in an overall stronger signal in the random-segregated compared to non-segregated condition16. If there are no color-selective symmetry channels, then all color-symmetry signals will be pooled into one single channel.”

How inappropriate the above quote is is easier to appreciate if we look at cases in which the physical and proximal configurations aren’t symmetrical, but the perceived configuration is. Take, for example, a picture of a parallelogram that looks like a slanted rectangle (as tends to be the case, e.g. in the three visible sides of the Necker cube). If the parallelogram is perceived as rectangular, then it looks symmetrical. This being the case, does it make sense to talk about “local symmetry signals” being summed up to produce the perceived symmetry? Isn’t the perception of the whole rectangle itself prior to and inextricably tied to the perception of its symmetry? If we are willing to invoke “local symmetry signals” then we could just as well invoke “local asymmetry signals,” since perceived asymmetry in a form is just as salient as symmetry - and just as dependent on prior organization. In perception (unlike in cognition), formal features such as symmetry are never disembodied; we never perceive “symmetry” as such, we perceive a symmetrical object. So, just as you can’t separate a shadow from the object that casts it, you can’t separate symmetry from the form that embodies it, and thus you can’t localize it.

The logical problem is the same whether or not the distal or proximal stimuli are symmetrical. For a given pair of dots in Gheorghiu et al’s stimuli to be tagged as a“local symmetry signal,” they must already have been perceptually incorporated in a perceived shape. Symmetry will be a feature of that shape, as a whole. It is therefore redundant to say that we perceive symmetry by going back and summing up “local signals” from the particular pairs of points that are matched only because they are already players in a global shape percept. If we don’t assume this prior organization, then any pair of dots in the stimuli are eligible to be called “symmetry signals” simply by imagining an axis equidistant from both.

In general, it isn’t reasonable or even intelligible to argue that any aspect of a shape, e.g. the triangularity of a triangle, is perceivable via a piecemeal process of detection of local “triangularity signals.” This was the fundamental observation of the Gestaltists; sadly, it has never sunk in.

In a subsequent post I will discuss the problem with the two alternative forced choice method used here. This method forces observers to choose one of two options, even if neither of those matches their perceptual experience. Here, I want to point out that this experiment is set up in precisely the same way: Data are used to choose among alternatives, none of which reflect nature.

On 2016 Nov 04, Lydia Maniatis commented:

Preliminary to a more general critique of this study, whose casual approach to theory and method is unfortunately typical in the field of vision science, I would like to point out the conceptual confusion expressed in the first few sentences of the introductory remarks.

Here, Gheorghiu et al (2016) state that "Symmetry is a ubiquitous feature in natural images, and is found in both biological and man-made objects...symmetry perception plays an important role in object recognition, [etc]."

If by "natural images" the authors are referring either to the retinal projection or to any projection of the natural or even man-made world, the statement is incorrect. It will be rare that the projection of either a symmetrical or an asymmetrical object will be symmetrical in the projection. The authors are making what the Gestaltists used to call the "experience error," equating the properties of the products of perception with the properties of the proximal stimulus.

Yes, the world contains may quasi-symmetrical objects, yes, man-made objects are, more often than not, symmetrical, and yes, we generally perceive physically symmetrical objects as symmetrical. But this not occurs not because the proximal stimulus mirrors this symmetry, but in spite of the fact that it does not.

The misunderstanding vis a vis the properties of the physical source of the retinal projection vs the properties of the projection vs the properties of the percept runs deep and is fundamental to studies that, like this one, treat perception as a "signal detection" problem.

When an observer says "I see symmetry" in this object or picture, this does not mean that the observer's retinal projection contains symmetrical figures (even if (and this is an insurmountable if) it were theoretically acceptable to treat the projection as being "pre-treated" by a figure-ground process that segregates and integrates photon-hits on the basis of the physical coherence of sources that reflected them).

So in what sense is symmetry being "detected"? Only in the sense that the conscious observer is inspecting the products of perceptual processes that occur automatically, and are the only link between conscious experience and the outside world. Because of this, an observer may "detect" symmetry in a perceptual stimulus even if the source of that stimulus is, in fact, asymmetrical. For example, when we look at a Necker cube, we "detect" symmetry, even though the figure that reflected the light is not symmetrical. When it comes to perception, the "feature detector" concept is a non-starter, because it ignores the nature of the proximal stimulation and mixes up cause and effect.

The fact that the authors use actually symmetrical figures as their experimental objects obscures this truth, of which they should be aware.

On 2016 Sep 19, Amit Dutt commented:

We thank the reader for the general appreciation and interest expressed in the TMC-SNPdb initiative. We agree that using tumor adjacent normal samples from cancer patients indeed has limitations to the effect as described in an unambiguous way in our article. In addition to our study, the Exome Aggregation Consortium (Lek M, 2016) –involving 7,601 normal blood samples derived from cancer patients of 60,706 normal samples studied— has similarly described the limitation in using such normal samples. Of note, the TMC-SNPdb is a pilot initiative project. As it evolves with the inclusion of additional normal samples, we do anticipate further refinements over the subsequent release/ versions of the database.<br> Unfortunately, the suggested comparison between the TMC-SNPdb with Sudmant et al. 2015 study cannot be made as Sudmant et al. (doi:10.1038/nature15394) performed a low pass whole genome sequencing at ~8x coverage to describe “structural alterations". Such low pass coverage studies are not ideally suited for variant analysis. However, in a separate study, the 1000 Genomes project consortium (1000 Genomes Project Consortium., 2015) has described whole exome sequence data of samples including data from >400 "normal" people of South-East Asian/Indian ethnicity at a mean high coverage of ~75x to exhaustively enlist the SNPs present in the population. Our study describing the TMC-SNPdb does compare and deplete the SNPs reported from this study to develop a unique set of yet undescribed SNPs specific to the Indian population, in an exclusive manner.

On 2016 Aug 31, Chandan Kumar commented:

This seems like a welcome initiative to generate a SNP database for Indian populations. However as noted in the discussion, use of tumor adjacent normal samples derived from cancer patients to generate a reference germline database is problematic. Interestingly, the 1000 genome project (Sudmant et al, An integrated map of structural variation in 2,504 human genomes,Nature 526,75–81,(01 October 2015), doi:10.1038/nature15394) includes data from >400 "normal" people of South-East Asian/Indian ethnicity. May be useful to compare the two datasets.

On 2016 Jul 25, Ram Dessau commented:

Discussion of formal criteria for website presentation, appear more important than medical or scientific issues in this commentary.

On 2016 Nov 02, Peter Hajek commented:

The finding that stop-smoking medications had beneficial rather than adverse effects on pregnancy outcomes is an important contribution. However, despite the claim in the Conclusion, the study does not really provide any information on their efficacy for smoking cessation. Medication users were trying to quit and an unknown but possibly large proportion of them were already non-smokers at intake (data on this crucial variable are not provided). The control group were all smokers. They were also not engaged in stop-smoking treatments and so likely to have a lower interest in quitting than those taking stop-smoking medications.

On 2016 Jul 13, Clive Bates commented:

The authors base their advice four main pillars, each of which is unreliable.

First, that we lack evidence of safety. We lack evidence of the complete safety of anything, including medicines, and notably those used in smoking cessation. What matters is the relative risk. We do have good evidence that e-cigarette vapour is much less hazardous than cigarette smoke [1]. Most of the hazardous agents in cigarette smoke are either not present at detectable levels in e-cigarette aerosol or at levels far below those found cigarette smoke. The authors mention diacetyl but fail the basic requirement of risk presentation, which is quantification - magnitude and materiality matter. The levels of diacetyl found in e-cigarettes (if it is used at all) are several hundred times lower than in cigarette smoke, and there are no known cases of 'popcorn lung' in smokers [2]. Overall, the Royal College of Physicians reviewed the safety of e-cigarettes and concluded [3]:

Although it is not possible to precisely quantify the long-term health risks associated with e-cigarettes, the available data suggest that they are unlikely to exceed 5% of those associated with smoked tobacco products, and may well be substantially lower than this figure". (Section 5.5 page 87)

Second, the authors argue that e-cigarettes may be ineffective as a smoking cessation aid. There are few RCTs evaluating these products because they are not medicines, but low-risk consumer alternatives to cigarettes. RCTs are not well suited to evaluating complex behaviour change in a rapidly evolving marketplace. However, there is considerable evidence of smokers using these products as alternatives to smoking and the studies cited by the authors are limited by confounding, selection bias and inappropriate aggregation of heterogeneous studies. May I suggest that interested clinicians cut through the thicket of claims and counterclaims, and read some of the accounts of smokers who's lives have been revolutionised by these products [4]? For the more cautious, e-cigarettes may be an option to suggest once the other options have been exhausted, but the approach certainly should not be discarded in its entirety.

Third, the authors argue that these products are not approved by the FDA and that there are fire and poisoning risks. Regulation by the FDA is no guarantee of safety - many medicines have severe side-effects and cigarettes are regulated by the FDA under the Tobacco Control Act. There have been a few cases of highly publicised e-cigarette battery fires - a small risk with all lithium-ion batteries. But this should be set against fire risks from smoking, which the National Fire Protection Service estimates causes the following damage [5]</p>

In 2011, U.S. fire departments responded to an estimated 90,000 smoking-material fires in the U.S., largely unchanged from 90,800 in 2010. These fires resulted in an estimated 540 civilian deaths, 1,640 civilian injuries and $621 million in direct property damage".

It is true that calls to poison centers rose 'exponentially' along with the growth of the product category from a low base. But the word 'exponential' does not mean 'large'. Calls to US Poison Centers amounted to 4,014 for e-cigarettes in 2014, but that compares with 291,062 for analgesics and 199,291 for cosmetics, and 2.2 million in total [6]. It is a small risk amongst many others common in the home.

Fourth and finally, the authors make a 'first-do-no harm" argument. But paradoxically they create potential serious harm with their chosen analogy:

Jumping from the 10th floor of a burning building rather than the 15th floor offers no real benefit.

This is an implied relative risk claim, which can be interpreted in two ways. First, that cigarettes and e-cigarettes are equally lethal (the likely result of jumping from the 10th and 15th floor is near certain death) or that e-cigarettes offer about two-thirds of the risk of smoking, based on the relative energy of impact (proportional to the distance fallen). Neither is remotely supportable by any evidence, but it this kind of casually misleading risk communication that is likely to cause fewer smokers to switch and more e-cigarette users to relapse. The debate about the relative risk of e-cigarette risk and smoking is better represented by a comparison of stumbling on the building's entrance steps with jumping from the 4th floor, the estimated height causing death in 50% of falls [7]. The weakness and inappropriateness of such analogies have been heavily criticised [8].

These metaphors, like other false and misleading anti-harm-reduction statements are inherently unethical attempts to prevent people from learning accurate health information. Moreover, they implicitly provide bad advice about health behavior priorities and are intended to persuade people to stick with a behavior that is more dangerous than an available alternative. Finally, the metaphors exhibit a flippant tone that seems inappropriate for a serious discussion of health science.

The responsible clinician should be providing accurate, realistic information and advice conveyed in a way that promotes understanding rather than unwarranted fear or confusion and helps the patient make an informed choice. It is important to recognise that smokers are at great risk, and if these products offer and attractive and appealing way out of smoking that works for them the clinician should not be a barrier to them taking that path.

[1] Farsalinos KE, Polosa R. Safety evaluation and risk assessment of electronic cigarettes as tobacco cigarette substitutes: a systematic review. Ther Adv Drug Saf 2014;5:67-86. [Link]

[2] Siegel M. New Study Finds that Average Diacetyl Exposure from Vaping is 750 Times Lower than from Smoking, The Rest of the Story, 10 December 2015. [Link]

[3] Royal College of Physicians, London. Nicotine without smoke:tobacco harm reduction, 28 April 2016 [Link]

[4] Consumer Advocates for Smoke-free Alternatives Associations (CASAA) User testimonials, accessed 12 July 2016 [Link]

[5] Hall J. The Smoking-Material Fire Problem, National Fire Protection Service, July 2013 [Link

[6] Mowry JB, Spyker DA, Brooks DE, et al. 2014 Annual Report of the American Association of Poison Control Centers' National Poison Data System (NPDS): 32nd Annual Report. Clin Toxicol 2015;53:962-1147. [Link].

[7] Marx J, Hockberger R, Walls R. Rosen's Emergency Medicine - Concepts and Clinical Practice, 8th EditionTable 36-1 page 290, August 2013. [Link]

[8] Phillips CV, Guenzel B, Bergen P. Deconstructing anti-harm-reduction metaphors; mortality risk from falls and other traumatic injuries compared to smokeless tobacco use. Harm Reduct J 2006;3:15.[Link]

Competing interests: I am a longstanding advocate for 'harm reduction' approaches to public health. I was director of Action on Smoking and Health UK from 1997-2003. I have no competing interests with respect to any of the relevant industries.

On 2016 Dec 07, Zvi Herzig commented:

The authors argue that their study Gmel G, 2016 is not cross-sectional because smoking was measured at the baseline. However, both the exposure (EC use) and the outcome (cessation) are measured simultaneously at follow-up. This allows for the most basic limitation of cross-sectional studies: reverse causality.

Contrary to the authors' understanding that findings demonstrate that vaping had no beneficial effect, the negative correlation between EC and cessation likely results from successful quitters lacking the need to initiate EC use.

Their fact that EC was rare at towards the beginning of the study only exacerbates the aforementioned flaw: those quit early on had little opportunity to expose initiate e-cigarette use as smokers and hence the lower e-cigarette use among tobacco quitters.

On 2016 Jul 19, Zvi Herzig commented:

None

On 2017 Dec 13, Daniel Mønsted Shabanzadeh commented:

Response to Frisch and Earp’s comments on Systematic Review

Daniel Mønsted Shabanzadeh^1,2,3 Signe Düring⁴ Cai Frimodt-Møller⁵

¹ Digestive Disease Center, Bispebjerg Hospital ² Research Centre for Prevention and Health, Capital Region of Denmark ³ Department of Clinical Medicine, Faculty of Health and Medical Sciences, University of Copenhagen ⁴ Mental Health Services of the Capital Region Region of Denmark ⁵ Department of Urology, CFR Hospitals, Denmark

This response was posted on the Danish Medical Journal's website July 2016: http://ugeskriftet.dk/files/response_to_frisch_and_earp_dmj.pdf

Dear Morten Frisch and Brian Earp

We thank you both for the comments(1) on our systematic review(2).

We respectfully disagree that the conductance of systematic reviews is unjustified. We can only emphasize the importance of identifying all available literature for clarity, before drawing conclusions on a delimited objective, such as, whether the exposure of circumcision has an impact on outcomes of perceived sexual function in adult males. The systematic process was performed according to the PRISMA statement and our conclusion reflected the lack of research in specific domains. We therefore, do not feel the need to justify the methodology any further.

You have problematized that we did not include a Canadian study of sexual partners to circumcised males, however, this was not part of our research objective. To answer the objective of the impact of circumcision on sexual partners perceived sexual function would require yet another systematic review process.

Circumcision is performed on both clinical indications such as penile or prepuce pathology and for nonclinical purposes such as cultural practice or with the aim of HIV-prevention. As we have demonstrated in the paper, many studies fail to distinguish these two populations which is major limitation from a clinical perspective, and one should therefore not draw conclusions about either from such studies. Frisch and Earp suggest that a number of other factors besides this clinical perspective may contribute to the outcome of perceived sexual function in males and we do agree. We have risen the issue of heterogeneity and limitations of the available literature in the discussion.

Our conclusion clearly states the results of the highest quality of available evidence and the lack of high quality studies on consequences of medically indicated circumcision and age at circumcision in order to fully answer our study objectives, and we have specifically stated that a majority of the studies does not take sexual orientation into perspective. We have suggested specific study designs on how to fill the gaps in evidence for future research.

We would like to extend to you both, and all other interested parties, an invitation to collaborate in the future. We can all agree that the field calls for further research, and would be happy to join forces, with contributions from both clinical, epidemiological and physiological angles.

References

(1) Frisch M, Earp B. Problems in the qualitative synthesis paper on sexual outcomes following nonmedical male circumcision by Shabanzadeh et al http://ugeskriftet.dk/files/201607001_commentary_frisch_earp_on_paper_by_shabanzadeh_et_al_dmj_1.pdf

(2) Shabanzadeh DM, During S, Frimodt-Moller C. Male circumcision does not result in inferior perceived male sexual function - a systematic review. Danish medical journal. 2016;63(7)

On 2017 Dec 06, Morten Frisch commented:

Problems in the qualitative synthesis paper on sexual outcomes following non-medical male circumcision by Shabanzadeh et al

by Frisch M^1,2 & Earp BD³

¹ Statens Serum Institut, Copenhagen, Denmark ² Aalborg University, Aalborg, Denmark ³ Hastings Center Bioethics Research Institute, USA

The comment below was published on the Danish Medical Journal's (Ugeskrift for Læger's) website on July 1, 2016: http://ugeskriftet.dk/files/2016-07-01_commentary_frisch_earp_on_paper_by_shabanzadeh_et_al_dmj_1.pdf

_____________________________________________________________________________________________________________

Shabanzadeh et al (1) claim in their title that “Male circumcision does not result in inferior perceived male sexual function.” Yet such a categorical conclusion does not follow from the data and analysis presented in the paper itself. As the authors state, there was “considerable clinical heterogeneity in circumcision indications and procedures, study designs, quality and reporting of results” in the studies they reviewed, which precluded an objective, quantitative assessment. Inadequate follow-up periods of only 1-2 years in the prospective studies imply that their results cannot be generalized beyond that range. In addition, “Risks of observer and selective reporting bias were present in the included studies … only half of the studies included validated questionnaires and some studies reported only parts of questionnaires.”

There is also a troubling heteronormativity to the authors’ headline claim. As they state: “Most studies focused on the heterosexual practice of intravaginal intercourse and did not take into account other important heterosexual or homosexual practices that comprise male sexual function.” Such practices include, inter alia, styles of masturbation that involve manipulation of the foreskin itself, as well as “docking” among men who have sex with men (MSM), both of which are rendered impossible by circumcision (2). Related to this, a recent Canadian study, not included in the paper by Shabanzadeh et al, found “a large preference toward intact partners for anal intercourse, fellatio, and manual stimulation of his partner’s genitals,” in a small but demographically diverse sample of MSM (3). Against such a backdrop, the authors’ characterization of their paper as “a systematic review” showing a definitive lack of adverse effects of circumcision on perceived male sexual function is unjustified. As Yavchitz et al argue, putting such a conclusive ‘spin’ on findings that are in truth more mixed or equivocal “could bias readers' interpretation of [the] results” (4). Thus, while the literature search performed by Shabanzadeh et al may well have been carried out in a systematic manner, their ‘qualitative synthesis without metaanalysis’ leaves the distinct impression of a partial (in both senses of the word)assessment.

The authors mention that the rationale for undertaking their analysis was “the debate on non-medical male circumcision [that has been] gaining momentum during the past few years”. But the public controversy surrounding male circumcision has to do with the performance of surgery on underage boys, specifically, in the absence of medical necessity. By contrast, therapeutic circumcisions that cannot be deferred until an age of individual consent are broadly perceived to be ethically uncontroversial, as are voluntary circumcisions performed for whatever reason on adult men, who are free to make such decisions about their own genitals (5). Consequently, studies dealing with either therapeutic or adult circumcisions are irrelevant to the ongoing controversy and should have been excluded by the authors in light of their own aims; such exclusion would have left only a handful of relevant investigations out of the 38 included studies.

As one of us has noted elsewhere: “the [sexual] effects of adult circumcision, whatever they are, cannot be simply mapped on to neonates” or young children (2). This is because studies assessing sexual outcome variables in adults typically do not account for socially desirable responding (6); they concern men who, by definition, actively desire to undergo the surgery to achieve a perceived benefit, and are therefore likely to be psychologically motivated to regard the result as an improvement overall; and such studies are typically hampered by limited follow-up (as noted above), rarely if ever extending into older age, when sexual problems begin to increase markedly (7). In infant or early childhood circumcision, by contrast, “the unprotected head of the penis has to rub against clothing (etc.) for over a decade before sexual debut. In this latter case … the affected individual has no point of comparison by which to assess his sexual sensation or satisfaction - his foreskin was removed before he could acquire the relevant frame of reference - and thus he will be unable to record any differences” (2).

The sexual consequences of circumcision are likely to vary from person to person. All-encompassing statements, such as that forming the title of the paper by Shabanzadeh et al, do not reflect this lived reality. Individual differences in sexual outcome variables will be shaped by numerous factors, such as the unique penile anatomy of each male, the type of circumcision and the timing of the procedure, the motivation behind it, the cultural context, whether it was undertaken voluntarily (or otherwise), the man’s subjective feelings about having been circumcised, his underlying psychological profile, and so on (8, 9). Collapsing across all of these factors to draw general conclusions can only serve to obscure such crucial variance (10).

Therefore, the choice of the authors to include any study looking at sexual outcomes after circumcision, whether in boys or adult males, whether in healthy individuals or in patients with a foreskin problem, whether in Africa or in Western settings, and whether with a follow-up period of decades or only a few months to years is problematic. Such a cacophony of 38 studies, dominated by findings on short-term sexual consequences of voluntary, adult male circumcision has limited relevance, if any, to the authors’ stated research question: how non-therapeutic circumcision in boys affects the sex lives of the adult men they will one day become.

References

(1) Shabanzadeh DM, Düring S, Frimodt-Møller C. Male circumcision does not result in inferior perceived male sexual function – a systematic review. Danish Medical Journal 2016; 63: A5245 (http://www.danmedj.dk/portal/page/portal/danmedj.dk/dmj_forside/PAST_ISSUE/2016/D MJ201607/A5245).

(2) Earp BD. Sex and circumcision. American Journal of Bioethics 2015; 15: 43-5.

(3) Bossio JA, Pukall CF, Bartley K. You either have it or you don't: the impact of male circumcision status on sexual partners. Can J Hum Sex 2015; 24: 104-19.

(4) Yavchitz A, Boutron I, Bafeta A, Marroun I, Charles P, Mantz J, Ravaud P. Misrepresentation of randomized controlled trials in press releases and news coverage: a cohort study. PLoS Med 2012; 9, e1001308.

(5) Darby R. Targeting patients who cannot object? Re-examining the case for nontherapeutic infant circumcision. SAGE Open 2016; 6: 2158244016649219.

(6) Earp BD. The need to control for socially desirable responding in studies on the sexual effects of male circumcision. PLoS ONE 2015; 10: 1-12.

(7) Earp BD. Infant circumcision and adult penile sensitivity: implications for sexual experience. Trends in Urology & Men’s Health 2016; in press.

(8) Goldman R. The psychological impact of circumcision. BJU International 1999; 83: 93-102.

(9) Boyle GJ, Goldman R, Svoboda JS, Fernandez E. Male circumcision: pain, trauma and psychosexual sequelae. Journal of Health Psychology 2002; 7: 329-343.

(10) Johnsdotter S. Discourses on sexual pleasure after genital modifications: the fallacy of genital determinism (a response to J. Steven Svoboda). Global Discourse 2013; 3: 256-265.

On 2017 Apr 07, Janelia Neural Circuit Computation Journal Club commented:

Highlight/Summary Howe and Dombeck imaged the activity in dopaminergic projection axons from the midbrain to the striatum during self-initiated locomotion and unexpected-reward delivery in mice. They reported a rapid increase in activity, which apparently preceded the locomotion onset. Rapid signalling in these axons was correlated with changes in acceleration during locomotion. Furthermore, axons that carried locomotion signals were found to be distinct from those that responded to unpredicted rewards. The authors concluded that distinct populations of midbrain dopaminergic neurons play a role in locomotion control and processing of unexpected reward.

Strengths This is one of a few studies that uses self-initiated locomotion to contrast dopaminergic signalling during movement-related activity and reward. By imaging separately from axonal projections originating in the substantia nigra (SNc) and ventral tegmental area (VTA), the authors found that the SNc signal was more ‘movement- related’, whereas VTA conveyed both movement and ‘reward-related’ signals. The authors confirmed this observation by describing a hitherto unknown gradient in locomotion associated signal versus reward signal along the dorsal-ventral axis of the striatum, which was consistent with a previously reported pattern of projections from the VTA and SNc to the striatum.

Weaknesses

There are several technical issues that complicates make the interpretation of these results difficult:

Detecting neural activity in individual axons using two-photon calcium imaging could be confounded by brain motion, which is expected to be exacerbated during locomotion. Electrophysiological recordings from the VTA and the SNc during locomotion and reward-delivery could have provided more unambiguous results. In fact, extracellular recordings from the SNc, recorded in a similar task, suggested that movement onset is represented by a pause in firing of SNc neurons (Dodson et al., 2016), rather than by an increase in firing rate.!

The authors reported that the dopaminergic signal preceded locomotion initiation by ~100 msec, as measured indirectly by treadmill acceleration. However, any postural changes or micro-movements, could have started before treadmill movement was detected. Therefore, whether movement initiation precedes or lags behind the dopaminergic signal is unclear based on this data, until more direct measurements of motion initiation are conducted (e.g. EMG, or detailed video analysis of the paws kinematics).

The authors claim that dopaminergic signalling during continuous locomotion were associated with changes in acceleration. However, during locomotion changes in acceleration had a rhythmic pattern at ~3.5 Hz, which complicates the interpretation of whether the dopaminergic signalling reflected past or future changes of the movement pattern. Furthermore, previous studies have reported oscillatory activity in the VTA at 4 Hz (Fujisawa & Buzsaki, 2011), and hence it is unclear whether the rhythmic signalling in the dopaminergic neurons during locomotion reported by Howe and Dombeck could simply reflect a coupling of the activity of the dopaminergic neurons to LFP.

On 2017 Jul 17, George McNamara commented:

more nuanced review at https://www.ncbi.nlm.nih.gov/pubmed/28481306

and compelling blog and Perspective blasting MTH1:

http://www.icr.ac.uk/blogs/the-drug-discoverer/page-details/call-to-bioscientists-choose-and-use-your-chemicai-probes-very-carefully

Blagg & Workman 2017 Cancer Cell (open access) http://dx.doi.org/10.1016/j.ccell.2017.06.005

On 2016 Aug 25, Morten Oksvold commented:

In figure 3E the micrograph of merged KI67 and DAPI staining does not correspond with the single DAPI staining.

A similar problem is also seen in figure 4D, where the PI-positive cells do not correspond with the hoechst stained cells. This is seen when you adjust the brightness. In this experiment, cells are exposed to 5 mg/ml PI for 30 min. The usual is to use 1 microgram/ml and study the cells directly, otherwise the PI will also stain the live cells.

On 2016 Jul 17, David Keller commented:

Berger's erroneous remarks in paragraph 4 imply possible serious errors in the Cologuard internal assay results

Berger wrote: "Dr. Keller’s attempt to draw a correlation between the occult hemoglobin value within a Cologuard test result and the stool hemoglobin concentration thresholds for positive results in a commercially available fecal immunochemical tests with separately validated reference points is just one example of how easily the erroneous use of data can yield potentially inappropriate clinical decisions. "

Keller: Each Cologuard specimen is subjected to an assay for occult hemoglobin concentration, measured in ng/mL, a measurement which must be accurate and repeatable by other modes of testing, including "commercially available fecal immunochemical tests (FIT)". Any biochemical measurement, such as fecal hemoglobin concentration, should remain constant and not vary depending on the test used to measure it. The Cologuard composite score requires an accurate measurement of fecal hemoglobin concentration, and it does not matter how that concentration is measured, but the concentrations measured by different tests must come out the same, within the error limits of the tests, or there is a problem.

Berger wrote: "For instance, as discussed at the FDA panel review of Cologuard, due to the Cologuard test’s use of significantly more stool in the Cologuard hemoglobin tube, the cut off of 100ng/mL concentration in the hemoglobin tube collection buffer used by some fecal immunochemical tests was estimated by FDA reviewers to be likely equivalent to more than twice that level within a Cologuard test."

Keller: Your statement is completely false, and reveals a serious misunderstanding of the very simple and basic concept of concentration itself. Assuming a homogeneous specimen, the concentration of a solute (in this case hemoglobin) is independent of the sample size. The fact that the Cologuard assay uses "significantly more stool" should not affect the measured hemoglobin concentration. The amount of collection buffer solution relative to the amount of stool specimen in the test tube should not make any difference. If two different assays are measuring different fecal hemoglobin concentrations for the same homogeneous sample, then one or both assays are erroneous. Because the commercial FIT assays are calibrated and validated by the FDA, while you admit that Cologuard's internal assays are not validated or calibrated to that standard, it appears that the internal Cologuard fecal hemoglobin concentration measurement is erroneous, which, in turn, impairs the accuracy of all Cologuard screens!

Berger wrote: "Even then, the theoretically resulting comparative threshold level is merely the product of conjecture because it has not been studied for that purpose, and to our understanding, the four most commonly used fecal immunochemical tests all generate only qualitative positive or negative results without release of the underlying quantitative information".

Keller: You are wrong - commercial FIT tests yield a BINARY result of positive or negative, which is completely QUANTITATIVE and not in any way qualitative. For example, the FIT test used as the control comparator in the Multitarget clinical trial [1] was positive for fecal hemoglobin concentrations greater than or equal to 100 ng/mL, and negative for lesser concentrations. The results of that FIT test were binary (positive or negative), quantitative, accurate, repeatable and did not vary with the size of the stool specimen! The results of the Cologuard internal fecal hemoglobin concentration assay had better agree with the FIT test results, or there is a serious problem, and it is probably in your assay (see my rebuttal of your second paragraph for a full explanation of why).

Reference

Imperiale, T.F., Ransohoff, D.F., Itzkowitz, S.H., Turnbull, B.A., Ross, M.E. Colorectal Cancer Study Group. Fecal DNA versus fecal occult blood for colorectal cancer screening in an average risk population. N Engl J Med. 2004 Dec 23;351 (270414. PubMed PMID: 15616205).

On 2016 Jul 16, David Keller commented:

Rebuttal of Berger's paragraph 3; and an explanation of how to define any test's normal range

Berger wrote: "Reporting of the constituent values within a Cologuard test is not only an unapproved use of Cologuard, but the granularity that individual marker levels and the specific composite score might be assumed to provide for clinical decision making in screening patients is not supported."

Keller: The result of any assay you run on my body tissues or wastes, regardless of the granularity or the FDA approval status of the assay, must be made available to me upon request. This is a right of any patient. Nothing you have said releases you from the obligation to inform me of my test results.

Berger wrote: "While the algorithm and the algorithm cut-off that define positive/negative are clinically validated for screening, the individual constituent values are not approved for clinical use outside the context of the algorithm.

Keller: According to the FDA, the Cologuard individual DNA assays are not approved for use outside the Multitarget algorithm primarily because Exact Sciences (your employer) did not apply for their approval, which is the necessary first step in the approval process. Every patient has the right to be informed of the results of any assay you run on his or her DNA, regardless of whether or not the assay is FDA-approved.

Berger wrote: "The component markers do not have individual “normal” reference ranges associated with them and, as a result, these intermediate analytes are not separately interpretable."

Keller: The normal range of any test may be defined as the average value of all test results, plus or minus 2 standard deviations, a range which will contain 95% of the results for the population. The remaining 5% may be defined as "abnormal".

Berger wrote: "This is different from the way that the separate tests ordered in a “test panel” can be interpreted, as under those circumstances, each test in the panel has its own separate reference range."

Keller: No, there is no difference, the process of defining a normal range is the same regardless of whether you are defining it for an internal Cologuard assay or a component of a "test panel".

Regardless of how or whether a reference range is defined, it does not alter the ethical imperative that you must release the result of any test you perform on a patient to that patient. In my original commentary, I presented two clinical scenarios where patients could come to harm because of the failure of Exact Sciences to report extreme or "abnormal" internal assay results, such as a high fecal hemoglobin concentration caused by a non-neoplastic colon disease, or a patient with a high-negative composite score who has a higher-than-average risk of false negative Cologuard screening result, and is given the same 3-year rescreening schedule as a patient whose fecal specimen result has the ideal lowest-risk composite score of zero. In the event that a patient comes to harm as a result of one of these clinical scenarios, Exact Sciences could, and should, become the target of a product liability lawsuit because of the failure to inform these patients of their abnormal internal assay results.

On 2016 Jul 12, David Keller commented:

Rebuttal of paragraph 2: Dr. Berger mistakes "binary" for "qualitative"

Berger: "The Cologuard test is intended for the qualitative detection of colorectal neoplasia associated biomarkers."

Keller: This so-called qualitative detection process is actually totally quantitative in nature. Each biomarker (DNA mutation, methylation abnormality or hemoglobin concentration) is carefully measured and inserted into a precise equation to generate a precise "Composite Score" which is directly related to the risk of colon cancer. This is a totally quantitative process.

Berger: " The numerical values generated from the component assays of the Cologuard test are excluded from the scope of the approval and are not clinically validated as individual test results."

Keller: I asked the FDA about that. Their reply to me was essentially as follows: the primary reason FDA did not approve the component assays as individual test results was that your company, Exact Sciences, did not apply for such approval. The first step of the FDA approval process for a test is for the manufacturer to apply for approval.

The MultiTarget algorithm was well validated at a composite score of 183 in a large randomized trial [1], which measured the risk of neoplasia (among other parameters) at that point. That validation can be extended across the entire range of "negative" Cologuard scores, from zero to 182, but clinical validation of one or more additional composite scores in that range is required. A reasonable minimum number of points to validate could be composite scores of zero, 60 and 120, thus providing (along with the already validated composite score of 183) approximation of the risk of neoplasia as a function of composite score by the three straight line segments defined by the risk of neoplasia at composite scores of zero, 60, 120 and 183. The mathematical name for this process is called "interpolation", and it will provide a reasonable estimate of neoplasia risk across the entire range of negative composite scores (0 - 182). The more points which are validated within that range, the more accurate the estimate of neoplasia risk will be across the entire range (as measured by root-mean-squared error).

Berger: "These numerical values are only constituents of the validated test algorithm that generates the qualitative Cologuard composite result (positive/negative)."

Keller: Numerical values are quantitative by definition. Your so-called "qualitative" result is derived from a number called the "composite score". The Cologuard result is "positive" if the composite score is 183 or greater, "negative" if the score is 182 or less. The Cologuard result is therefore not qualitative, it is binary. Dr. Berger has clearly mistaken a binary decision-making process for a qualitative one. This is a clear-cut error of nomenclature and conceptualization, for which I will submit an erratum to this journal.

Reference

1: Imperiale, T.F., Ransohoff, D.F., Itzkowitz, S.H., Turnbull, B.A., Ross, M.E. Colorectal Cancer Study Group. Fecal DNA versus fecal occult blood for colorectal cancer screening in an average risk population. N Engl J Med. 2004 Dec 23;351 (270414. PubMed PMID: 15616205).

On 2016 Jul 12, David Keller commented:

Beyond rebuttal: constructive suggestions for unleashing the full power of ColoGuard screening

My point-by-point rebuttal of the response by Dr. Berger and Dr. Lidgard to my commentary is necessary but of little importance. What is important is that their company's outstanding colon cancer screening system, an implementation of the MultiTarget algorithm marketed under the commercial name "ColoGuard", could function at an even higher level of accuracy if its full power were unleashed for each fecal sample screened.

I propose that the Composite Score be used for risk-stratification of "negative" ColoGuard screens, so that we do not perpetuate the potentially dangerous situation we have now, where patients with Composite Scores ranging from zero to 182 are all treated the same: they are told their result is negative, nobody is certain when to repeat the test, but Medicare will pay for it again in 3 years. However, a composite score of 182 must confer a higher risk of being a false negative than a score of zero. Further, a composite score of 183 is only 0.5% higher than a score of 182, yet a patient with a score of 182 is told their screening result is negative and sent home, while a patient with score 183 is told he needs a colonoscopy immediately. That kind of discontinuity, called a Heaviside step function, is not found in nature. The risk of cancer must, as a natural phenomenon, vary across the range of composite scores in a manner which is smooth and continuous.

In a large randomized clinical trial, Cologuard was found to have a sensitivity of 92.3% for detecting colorectal cancer, and hence, a false-negative rate of 7.7%. The Cologuard assays for malignancy-associated DNA yield results which are directly related to cancer risk, so the risk of a false-negative result must therefore vary directly with the composite score, increasing monotonically over the range of negative composite scores, from zero to 182. In other words, across the range of zero to 182, any composite score of N+1 must confer an incrementally higher risk of false-negative colon cancer than is conferred by a composite score of N. Therefore, patients whose Cologuard screening result is currently reported simply as "negative" can be further risk-stratified by their composite scores, for example:

Score.........Repeat screening interval

0 - 60........Repeat Cologuard in 3 years

61 - 120......Repeat Cologuard in 2 years

121 - 182.....Repeat Cologuard in 1 year

The retail price of one Cologuard test kit is $649, very expensive compared with standard fecal immunochemical screening for colon cancer, which retails for $15 per kit. Risk-stratification would concentrate medical resources where the risk is highest, by allocating additional Cologuard kits to patients at the highest risk of an initial false-negative screen. At the same time, fewer false positive screens would occur, compared with simply repeating the Cologuard screen annually for all patients.

Validation of the composite score across its entire negative range of zero to 182, and determination of where to position the break points in composite score for optimal risk stratification, can be performed using Monte Carlo simulation, with models based on post-approval Cologuard clinical data. Similar techniques were employed by CISNET to compare the outcomes of various screening algorithms, and these simulation results were recently published in JAMA, to support the latest USPSTF colon cancer screening recommendation update [1]. These results can also be applied to hybrid screening strategies, devised in response to spending limits or other constraints [2].

References

1: Knudsen AB, Zauber AG, Rutter CM, Naber SK, Doria-Rose VP, Pabiniak C, Johanson C, Fischer SE, Lansdorp-Vogelaar I, Kuntz KM. Estimation of Benefits, Burden, and Harms of Colorectal Cancer Screening Strategies: Modeling Study for the US Preventive Services Task Force. JAMA. 2016 Jun 21;315(23):2595-609. doi: 10.1001/jama.2016.6828. PubMed PMID: 27305518.

2: Keller DL. A Hybrid Non-Invasive Colon Cancer Screening Strategy, To Maximize Sensitivity With Medicare Coverage. PubMed Commons, accessed on 7/30/2016 at the following URL:

http://www.ncbi.nlm.nih.gov/pubmed/27305518#cm27305518_22819

On 2017 Jun 09, Lydia Maniatis commented:

The trigger for choosing this article to comment on was the reference in the title to “low-level mediation.” It reflects one of the deadly sins of contemporary vision science, i.e. the invalid assumption that aspects of perceptual experience may be directly attributed to the activities of particular sets of neurons in particular, anatomically early (more closely linked to the retina) areas of the visual system.

One problem with such a view is that the activities of neurons in these areas, (like the retinal cells themselves, and, arguably, all the neurons in the visual system and beyond) are the physiological basis for all aspects of the percept. Thus, it doesn’t make sense to specially attribute, e.g. the movement of a grey dot to the special sensitivities of neural population x, when these underlie both the perception of the grey dot, the background, the relative position of dot and frame, and every other feature of the percept. Such claims are, in other words, arbitrary and cannot be corroborated by ascertaining what subjects are seeing.

The most popular area to invoke in this respect is, as is the case here, area V1. The reason is historical; Hubel and Wiesel’s work on the striate cortex (corresponding to V1) of cats and later monkeys. They reported on the relative firing rates of neurons to straight bars differing in orientation, length, direction of movement. These results were over-interpreted to mean that neurons in V1 were akin to specialized detectors of the particular stimuli, within the narrow set tested, which made them fire fastest. However, as Teller (1984) noted in her critique of common psychophysical linking propositions, a. we know that the neural code is not based on maximum, but relative, firing rates, b. there is an infinitely large equivalence class of stimuli that would cause these same neurons to fire.

Nevertheless, investigators keep the flawed, fragile story flickering by employing stimuli and conditions whose results may be, though loosely and permissively, interpreted according to such crude assumptions. That the story is woefully inadequate (that investigators don’t know what factors to control so as to, at least, consistently interpret results) is reflected in the perennial admission, as in this article, that psychophysical experiments get conflicting results which investigators are unable to rationalize:

“Differences in the outcomes of different psychophysical procedures have already been noted elsewhere, and perhaps deserve more attention…

“Although our manipulation of attention did not produce a directional aftereffect, Lankheet and Verstraten’s (1995) manipulation of attention did. The reason for this discrepancy remains unclear…” Morgan et al (2016, p. 2630).

“…our results (Exp 4) did not confirm the factual basis for the claim (Blaser et al , 2005) that a 90 degree probe…we cannot be certain why our results are different…Differences include the psychophysical method (2AFC rather than MSS…), the statistical methods of analysis, the use of colors that appeared equally salient to the observer….”

If the authors are saying that even the statistical methods of analysis can potentially produce opposing interpretations of data, but investigators don’t understand how or why, what can possibly be the theoretical value of their own data/interpretations? How are we supposed to evaluate these things, if theoretical control of conditions is so inadequate and interpretation of experimental results so mystifyingly wide open and susceptible to inexplicable “butterfly effects”?

On 2016 Aug 24, Mike KLYMKOWSKY commented:

The cilia of prokaryote is a completely different structure from that of a eukaryote. This makes the first sentence of the abstract obscure to say the least.

On 2017 Nov 30, Natalie Clairoux commented:

Free version of this article available after May 31, 2018 at https://papyrus.bib.umontreal.ca/xmlui/handle/1866/19673

On 2017 Mar 23, University of Kansas School of Nursing Journal Club commented:

Team Members: Hayley Janner, Annie Yungmeyer, Katherine Barnthouse, McKenzie Baker, Dylan Severson, Macy McKee [Class of 2017]

Background

Our team selected this article due to the significant role that workplace bullying plays in establishing and maintaining a healthy work environment. Nursing had been historically associated with high rate of workplace bullying, especially towards new or inexperienced nurses--best known by the common expression “nurses eat their young.” Because of this reputation, the effect of bullying on work environments and nursing satisfaction should be explored. 

Thus, this study fills a vital gap in the literature by examining both the causes and effects of workplace bullying in the microsystem. This article applies to several of the modules for processes of a healthy work environment, including authentic leadership, as Yokohoma et al. (2016) found that lack of authentic leadership contributes to a work environment that fosters bullying, and creating a motivating environment, as workplace bullying has been found to be acutely and chronically demotivating for nurses.

Methods

This article was found via a literature search of CINAHL. The study design was a cross-sectional design and data was collected via a distributed self-administered questionnaire. The questionnaire was distributed to nurses in Japan attending various nursing conferences, all of which were unaffiliated with any nursing workplaces. The survey distributed consisted of the Negative Acts Questionnaire-Revised (NAQ-R), which assesses for workplace bullying behaviors, and the Practice Environment Scale of the Nursing Work Index (PES-NWI), which assesses quality of work environment. Participant demographics and other workplace factors (such as average hours of overtime work, average days off in a month, opportunity to request work off, and more) were also collected in the questionnaire (Yokohama et al., 2016). The issue of workplace bullying impacts all nurses in all areas of the world. However, because the population surveyed was Japanese nurses, this study directly represents the work environments of Japanese nurses. Nonetheless, this study is still significant as the results of this study could generate a starting point for researchers in other countries studying the relationship of workplace bullying and a healthy work environment.

Findings

The study found that workplace bullying in Japan is a significant issue, as 18.5% of participants were classified by survey responses as being a victim of bullying. Bullying was considered to have taken place when participants reported that any negative behavior mentioned in the NAQ-R was directed towards them either on a “weekly” or “daily” basis. The most common bullying behaviors that took place were “someone withholding information that affects your performance,” “being exposed to an unmanageable workload,” and “being shouted at or being the target of spontaneous anger (or rage)” (Yokohama et al., 2016, p. 2481). Demographic and workplace factors determined to be associated with being a victim of bullying included being “unmarried, holding a bachelor’s degree or higher, having registered nurse and additional qualifications, fewer years of nursing experience, fewer years of experience in current workplace, more overtime hours per day, not always having the opportunities to request days off, working on more days off, and a less HWE (defined by lower than average scores on the five PES-NWI subscales)” (Yokohama et al., 2016, p. 2481-2482). Workplace bullying was also associated with lower scores on the nurse manager section of the PES-NWI, including leadership, ability, and support of nurses.

There are several limitations with this study. One limitation was the cross-sectional design of the study, which prevented the authors from proving causal factors for bullying--only correlational factors can be described. Secondly, because the study was personally answered by nurses, results may be subjective depending on the nurses’ mindset and personal evaluation of appropriate workplace conduct and bullying, among other factors. Finally, this study was performed exclusively via surveying of Japanese nurses. Thus, while the study may be representative of workplace bullying in Japanese nursing environments, it may not be possible to generalize this to all nursing workplace bullying.

Implications

Workplace bullying is an important issue in nursing due to the numerous negative consequences it has been linked with, most importantly with nurse retention, satisfaction, nurse depression and lowered quality of patient care. Nurse depression contributes to burnout and frequent turnover, adding to the ever-rising costs of the healthcare industry. Additionally, depression can result to decreased patient care quality leads to increased medical error and negative patient outcomes. Thus, workplace bullying in nursing is a vital issue that needs to address, as its consequences run contrary to the purpose of medicine and nursing as a whole.

This issue is important to us on a personal level as graduating nursing students since we came into nursing to help and heal patients because we care deeply about them. This caring values and attitudes should extends to our coworkers as well. It is utterly unacceptable to comprehend that a significant number of individual in an industry known for helping people heal instead choose to tear each other down. Our efforts should be focused instead on banding together to provide not only the best care possible to patients, but to care and nurture each other—the same reason that majority of us in nursing entered the industry. 

This study is also important in presenting the importance of the microsystem leadership development and the leadership role implications on the contribution of poor nursing leadership to workplace bullying. In their study, Yokohama et al. (2016) found that individuals who scored their managers low on leadership, ability, and support of nurses were more likely to be victims of workplace bullying. In the PES-NWI, leadership specifically is comprised of five items that are similar to traits held by authentic leaders. Nurse Managers who are not effective leaders are less effective at dismantling a culture of bullying on their unit. Thus, development of authentic leadership in nurse managers carries the possibility of reducing workplace bullying that nurses experience.

This article contributes greatly to our future nursing practice because it has clearly displayed to us the far-reaching impact that poor leadership can have on several unit factors, such as inability to change a toxic and bullying workplace culture leading to poor patient outcomes. This publication has re-emphasized to us the importance of practicing authentic leadership in our own careers, especially if we advance into leadership positions such as nurse manager. Finally, we will not turn a blind eye to workplace bullying in my own future employment, as the consequences for patients are simply not acceptable.

References Yokoyama, M., Suzuki, M., Takai, Y., Igarashi, A., Noguchi-Watanabe, M. and Yamamoto- Mitani, N. (2016). Workplace bullying among nurses and their related factors in Japan: a cross-sectional survey. Journal of Clinical Nursing, 25: 2478–2488. doi:10.1111/jocn.13270

On 2016 Sep 19, Prashant Sharma, MD, DM commented:

Quoted from the abstract above, "Following WHO recommendations, refractory anemia with excess blasts (RAEB)-2 diagnosis is not possible in MDS-E, as patients with 10% to < 20% BM blasts from TNCs fulfill erythroleukemia criteria".

Err... where would WHO 2008 place a case with 51% erythroid cells and 3% blasts with Auer rods that's negative for the leukemia-defining recurring genetic abnormalities?

On 2016 Sep 19, Prashant Sharma, MD, DM commented:

Very interesting... This would certainly upgrade more than a few cases. Hopefully the WHO is listening, and other large centres are reanalyzing their marrow differentials for confirming/refuting this "game-changing" paper.

What about the blast% in remission status marrows from acute leukemia patients? Its currently mostly done from TNCs, but based on this study is it possible that calculating it from NECs would provide better prognostication?

• Prashant Sharma, Assoc. Prof. of Hematology, PGIMER, Chandigarh, India

On 2016 Aug 27, Santosh Kondekar commented:

It was interesting to read about pathogenesis of COPD. Its really beautifully differentiated from asthma. The concept of early child hood onset of COPD needed an extra mention. As COPD of early onset often has its roots in early childhood.An early onset COPD often has some neonatal or infantile insult that causes fixed parenchymal insult which makes the airways more susceptible for dysplasia or remodelling. As these cases are often overlooked as refractory child hood asthma; they often are mistreated; early picking up of low FEV1 and non responsiveness to steroids should compel a clinician take an appropriate step like a CT chest at early age to pick up fixed parenchymal damage or fixed airway changes. Clinically; to avoid overdiagnosis of asthma; we follow a criteria called "other than asthma" or OTA criteria; this helps us segregate cases with potential for development of COPD in future. OTA can be read at http://childasthma.weebly.com/ota-other-than-asthma-or-asthma-like-illnesses.html

On 2016 Sep 20, Lydia Maniatis commented:

Please see comments on PubPeer.

On 2016 Jul 14, David Keller commented:

The placebo effect is mediated via the very same neural pathways damaged in Parkinson's disease

Neural imaging studies have demonstrated that the placebo effect in healthy subjects is mediated by the same neural pathway damaged in Parkinson disease (PD), namely the transport and release of dopamine from the substantia nigra to the striatum.[1] This is why placebos of all types can cause surprisingly robust and durable clinical improvements in PD. The authors of this anecdotal case note that meditation has been shown to release dopamine in the striatum. The questions include: does meditation release more dopamine than placebo? What is an effective placebo control for meditation, and how can it be distinguished or truly differ from real meditation? How can subjects be instructed to meditate or placebo-meditate in a double-blinded fashion? and so on. The hypothesis that meditation might cure, remit, or benefit PD patients in any way more so than placebo seems difficult if not impossible to test. For people with Parkinson's who doze off when they try to meditate, it may at least be helpful in inducing drowsiness, which in turn can increase their sleep benefit.

Incidentally, there was no indication for a DaT scan in this patient, whose clinical diagnosis of Parkinson's disease was indisputable at the time the scan was done. I point this out because the DaT scan selectively delivers 21 times as much ionizing radiation to the striatum than does a standard CT scan of the whole brain.[2]

References

1: de la Fuente-Fernández R, Lidstone S, Stoessl AJ. Placebo effect and dopamine release. J Neural Transm Suppl. 2006;(70):415-8. Review. PubMed PMID: 17017561.

21: Keller DL. Proposal for a clinical trial to test the safety of a widely-used radionuclide scan. Comment on PMID: 26236969. In: PubMed Commons [Internet]. 2015 Sept 15 [cited 2015 Nov 20]. Available from http://www.ncbi.nlm.nih.gov/pubmed/26236969#cm26236969_11818

On 2017 Mar 08, Martin Mayer commented:

Reply to Dong D. Wang, MD, ScD and Frank B. Hu, MD, PhD

Author: Martin Mayer, MS, PA-C

Conflict of interest: None

I sincerely appreciate the reply from Drs. Wang and Hu, including the time they took to read my original commentary on their study and the time they took to compose a response. However, their reply ultimately does not resolve the issues I present in my original commentary, and I am concerned they may mistakenly believe I am attempting to dismiss entirely the field of nutritional epidemiology or the potential benefits of a sound diet; neither of these are true, and nothing herein or in my original commentary should be construed as a suggestive, definitive, or de facto exoneration or dismissal of various patterns of fat intake or dietary composition. Such impressions would suggest having missed the central thrust behind my original commentary, namely (1) researchers should always endeavor to provide balanced and objective qualitative and quantitative context for their research findings, and (2) those reading research articles should consider these issues during evidence appraisal, synthesis, translation, and application. Nevertheless, and even though I am a strong advocate for healthy lifestyles (including a sound diet), I stand by my original commentary, and I respond here in a point-by-point fashion.

(Post edited after original posting to update the link to my reply, as it was not displaying correctly.)

Note: I edited this post and my full reply to Wang and Hu on September 14, 2017 to update all URLs hyperlinking to my original commentary due to a rebranding of the website on which my blog post appears. I did not make any other changes to this post (I even include the originally-present parenthetical note about editing the original post due to issues with how my reply was displaying) or my full reply. The original post appears below in its original form for the sake of completeness and transparency of the record, as does the original link to my full reply to Wang and Hu.

-----------------------Begin original post from March 8, 2017-----------------------

Reply to Dong D. Wang, MD, ScD and Frank B. Hu, MD, PhD

Author: Martin Mayer, MS, PA-C

Conflict of interest: None

I sincerely appreciate the reply from Drs. Wang and Hu, including the time they took to read my original commentary on their study and the time they took to compose a response. However, their reply ultimately does not resolve the issues I present in my original commentary, and I am concerned they may mistakenly believe I am attempting to dismiss entirely the field of nutritional epidemiology or the potential benefits of a sound diet; neither of these are true, and nothing herein or in my original commentary should be construed as a suggestive, definitive, or de facto exoneration or dismissal of various patterns of fat intake or dietary composition. Such impressions would suggest having missed the central thrust behind my original commentary, namely (1) researchers should always endeavor to provide balanced and objective qualitative and quantitative context for their research findings, and (2) those reading research articles should consider these issues during evidence appraisal, synthesis, translation, and application. Nevertheless, and even though I am a strong advocate for healthy lifestyles (including a sound diet), I stand by my original commentary, and I respond here in a point-by-point fashion.

(Post edited after original posting to update the link to my reply, as it was not displaying correctly.)

On 2017 Feb 14, Lydia Maniatis commented:

"Our findings are consistent with ... biological plausibility...." "Plausibility" is quite a low and rather subjective bar; an argument against outright rejection, not an argument in support of...

On 2017 Feb 11, Dong Wang commented:

Reply to Martin Mayer, MS, PA-C

Authors: Dong D. Wang, MD, ScD and Frank B. Hu, MD, PhD

From the Departments of Nutrition (DDW and FBH) and Epidemiology (FBH), Harvard T. H. Chan School of Public Health, Boston, MA; The Channing Division for Network Medicine, Department of Medicine, Brigham and Women’s Hospital and Harvard Medical School, Boston, MA (FBH)

We agree with Mr. Mayer that ‘well-designed, well-executed randomized controlled trials (RCTs)’ can provide strong evidence for the causal effect between dietary fatty acids and mortality. However, because of multiple methodological limitations, e.g., poor compliance and high drop-out rate, decades-long RCTs testing effects of dietary interventions on hard endpoints, such as cardiovascular disease (CVD) incidence and mortality, are extremely difficult to conduct [1]. High cost and ethical considerations are additional challenges for conducting such a RCT. Further, the notion that RCTs are ‘confounding-free’ is only held when there are low rates of drop out and high degree of compliance. In most large-scale long-term RCTs, biases may occur after baseline randomization due to differential adherence to assigned treatment regimens, differential loss to follow-up, and other differences between comparison groups [2]. In addition, our findings based on prospective cohorts are consistent with effects of replacing saturated fatty acid (SFA) by polyunsaturated fatty acid (PUFA) on both blood lipids [3] and cardiovascular disease [4] from RCTs. Thus, in most situations, large prospective cohort studies of hard clinical endpoints, when well designed and interpreted in the context smaller RCTs on intermediate endpoints such as blood lipids, can provide the best available evidence to inform dietary recommendations. One such example is trans fat. Large epidemiologic studies like ours found a consistent positive association between trans fat intake and risk of cardiovascular disease. Meanwhile, small RCTs found that trans fatty acids increase total and LDL cholesterol. The combination of these two types of evidence has led to the policies that result in food labeling and banning in the food supply [5].

Citing Nissen and Ioannidis’ attacks on methodological issues of nutritional epidemiology [6, 7], Mr. Mayer questioned the validity of the food frequency questionnaires (FFQs) in assessing dietary intakes. However, Nissen and Ioannidis’ viewpoints and Mr. Mayer’s question simply reflect lack of understanding of the basic methodology of nutritional epidemiology and human nutrition research. In contrary to Mr. Mayer’s claim, our food frequency questionnaires (FFQs) have been demonstrated to be a useful and valid dietary assessment instrument to measure long-term usual dietary intake in well-conducted epidemiological studies [1, 8]. The validity of our FFQs against multiple-day diet records and biomarkers in the validation studies has been extensively documented [8]. For example, the correlations between energy-adjusted intakes assessed by the 1986 FFQ and the mean of multiple weighed 1-week dietary records collected in 1980 and 1986, corrected for variation in the records, were 0.67 for total fat, 0.70 for SFA, 0.69 for MUFA, and 0.64 for PUFA. [8] Correlations increased when the mean of 3 FFQs (1980, 1984, and 1986) was used; for example, for SFAs the correlation was 0.95. The correlation between dietary fatty acid intake assessed by the FFQ and the composition of fatty acids in adipose tissue were 0.51 for TFA, 0.35 for LA, and 0.48 for long-chain n-3 PUFA in NHS, [9] and 0.29 for TFA, 0.48 for LA, and 0.47 for EPA in HPFS. Moreover, adjustment for total energy intake, along with use of cumulative average intake calculated from many repeated FFQs, further dampens the measurement errors and improves the validity [8].

By pointing out that our study population was ‘exclusively health care professionals with noteworthy exclusion criteria’, Mr. Mayer questioned the generalizability of our findings. However, the effect estimates represent the underlying physiological mechanisms relating fatty acid intake to mortality that are generally applicable to other populations. In addition, for the estimated effect of substituting SFA by PUFA, the hazard ratio (HR) of CVD mortality in our study (0.72, 95% CI, 0.65-0.80) is similar to the HR of coronary death (0.74, 95% CI, 0.61-0.89) estimated from a pooled analysis including 11 cohorts with diverse sociodemographic characteristics, which further support the generalizability of our findings [10]. Because our study intended to mimic a primary prevention setting, we excluded participants with major chronic diseases, including CVD, cancer and diabetes, at baseline. In contrary to Mr. Mayer’s assertion, applying these exclusion criteria, our study produced more generalizable findings to inform dietary recommendations for primary prevention of disease outcomes in the general population.

Mr. Mayer criticized our use of HR, a ratio measure, and claimed only reporting HRs is ‘considerably less informative and can contribute to distorted appraisal of research findings’. These assertions are unfounded. Both ratio and difference measurements have their own merits and usefulness. Difference measures are measures of the public health and clinically relevant effect of exposure, whereas relative measures are measures of the biological strength of the association between an exposure and disease outcome. Therefore, reporting HRs is compatible with the objective of our study, i.e., to examine the associations of specific dietary fats with total and cause-specific mortality. From a technical perspective, HR is the default outputs estimated by the multiplicative Cox proportional hazards model, the most robust and widely applied statistical model for time-to-event data. It is important to note that HRs can be compared across different studies and populations, whereas difference measures are difficult to compare because of different baseline risk in different populations.

In summary, our study provided strong evidence because of the solid study design, such as many repeated measurements of diet, validated measurement methods and high follow-up rates over decades, and sophisticated statistical analysis, i.e., extensive adjustment for a large number of potential confounding factors. Our findings are consistent with other high-quality evidence from both observational cohort studies and RCTs [3, 4, 10] and meet multiple key Bradford-Hill criteria, including the strength and consistency of the evidence, biological plausibility, temporal relationships and experimental evidence on intermediate biomarkers.

Conflict of interest: None

Reference

[1] Satija, A., et al., Advances in nutrition, 2015. 6(1): p. 5-18.

[2] Manson, J.E., et al., Jama, 2016. 315(21): p. 2273-4.

[3] Mensink, R.P., et al., The American journal of clinical nutrition, 2003. 77(5): p. 1146-55.

[4] Mozaffarian, D., et al., PLoS Med, 2010. 7(3): p. e1000252.

[5] National Conference of State Legislatures.: http://www.ncsl.org/issues-research/health/trans-fat-and-menu-labeling-legislation.aspx.

[6] Ioannidis, J.P., BMJ, 2013. 347: p. f6698.

[7] Nissen, S.E., Annals of internal medicine, 2016. 164(8): p. 558-559.

[8] Willett, W.C., Nutritional epidemiology 2013, Oxford University Press.

[9] London, S.J., et al., The American journal of clinical nutrition, 1991. 54(2): p. 340-5.

[10] Jakobsen, M.U., et al., The American journal of clinical nutrition, 2009. 89(5): p. 1425-32.

On 2017 Jan 14, Martin Mayer commented:

Reporting and appraising research: a cautionary tale

Substituting various fats for carbohydrates or saturated fat: an uncertain recipe missing quantitative context and a cautionary example of reporting and appraising research

Broadly speaking, science is a way of thinking that involves asking answerable questions about phenomena and then systematically and impartially pursuing means to reduce uncertainty about the answer as much as possible. During the pursuit, findings must always be appropriately contextualized to avoid inaccurate, disproportionate, or otherwise mistaken interpretations, as such mistaken interpretations run contrary to the raison d’être of scientific inquiry. Unfortunately, confusion about and mistaken or overreaching interpretations of research abound.

Wang and colleagues recently published an article in JAMA Internal Medicine investigating various patterns of fat intake on total and cause-specific mortality. Their article speaks to the above and will add tangibility to the above considerations; it therefore serves as an instructive example to be considered in some detail, but the concepts considered herein are certainly more broadly applicable.

Read the rest here (http://blogs.bmj.com/bmjebmspotlight/2016/10/03/reporting-and-appraising-research-a-cautionary-tale/).

Note: I edited this post on September 14, 2017 to update all URLs hyperlinking to my original commentary due to a rebranding of the website on which my blog post appears. I did not make any other changes. The original post appears below in its original form for the sake of completeness and transparency of the record.

-----------------------Begin original post from January 14, 2017-----------------------

Reporting and appraising research: a cautionary tale

Substituting various fats for carbohydrates or saturated fat: an uncertain recipe missing quantitative context and a cautionary example of reporting and appraising research

Broadly speaking, science is a way of thinking that involves asking answerable questions about phenomena and then systematically and impartially pursuing means to reduce uncertainty about the answer as much as possible. During the pursuit, findings must always be appropriately contextualized to avoid inaccurate, disproportionate, or otherwise mistaken interpretations, as such mistaken interpretations run contrary to the raison d’être of scientific inquiry. Unfortunately, confusion about and mistaken or overreaching interpretations of research abound.

Wang and colleagues recently published an article in JAMA Internal Medicine investigating various patterns of fat intake on total and cause-specific mortality. Their article speaks to the above and will add tangibility to the above considerations; it therefore serves as an instructive example to be considered in some detail, but the concepts considered herein are certainly more broadly applicable.

Read the rest here (http://blogs.bmj.com/ebm/2016/10/03/reporting-and-appraising-research-a-cautionary-tale/).

On 2017 Jun 28, Randi Pechacek commented:

Elisabeth Bik wrote a brief overview of this paper on microBEnet.

On 2016 Aug 19, Venkatesh Thiruganasambandamoorthy commented:

Thanks to QxMD and Dr. Schwartz for bringing it to end users as a convenient app

On 2016 Aug 02, Daniel Schwartz commented:

The Canadian Syncope Risk Score can be accessed at the point of care using mobile & web app 'Calculate'

http://www.qxmd.com/calculate/calculator_383/canadian-syncope-risk-score-csr

Conflict of interest: Medical Director, QxMD

On 2017 Sep 19, Harri Hemila commented:

A manuscript version is available at HDL.

On 2016 Sep 11, Johannes W. Dietrich commented:

We got feedback from readers that SPINA-GT and SPINA-GD are difficult to calculate. There is free software available from http://spina.sf.net that can calculate SPINA parameters and Jostel's TSH index from equilibrium concentrations of TSH, free T4 and free T3. In addition, software for using the UCLA platform is available on request from the UCLA Biocybernetics Laboratory.

On 2016 Jul 15, Anthony Jorm commented:

In their response to the letter by Jorm et al which questioned whether scaling up of treatment is likely to reduce prevalence of depression and anxiety Jorm AF, 2016, Chisholm and colleagues commented that “population ageing… in many contexts will cancel out or more than counteract the impact of treatment” Chisholm D, 2016. As far as high income countries are concerned, this is unlikely. A review of age group differences in the risk of anxiety and depression found that the evidence supported a reduction of risk with older age Jorm AF, 2000. These findings imply that population ageing is unlikely to counteract the impact of increased provision of treatment on the prevalence of depression and anxiety in high-income countries.

On 2016 Jul 27, Kerin Tyrrell commented:

This article can also be viewed and/or downloaded from an author's personal web site:

https://is.gd/CQP1TZ

On 2016 Aug 27, Nisha G Arya commented:

We reran the meta-analysis using the new version of GingerALE (2.3.6). We got the exact same coordinates as our previous analysis, except that the midbrain and pons were not longer identified as significantly activated. In our discussion of the paper, we had already mentioned that the midbrain and pons are difficult to image, so these new results are not surprising.

On 2016 Aug 09, Christopher Tench commented:

The version of GingerALE used (2.3.1) had a bug that results in false positive results. The bugs were fixed at versions 2.3.3 and 2.3.6

On 2016 Oct 28, Wichor Bramer commented:

I spotted a very small error that might lead to confusion in table 1: In C3 it says: "Review the top references without page numbers and those with page numbers, starting with number 1 for equivalent author names."

We meant: "Review the top references, those without page numbers and those with page numbers starting with number 1, for equivalent author names."

It is not necessary to review all references manually. Only the references that lack a page number, or the ones starting with 1 (1-3, 1-27 etc) can potentially contain false duplicates, and should be checked manually.

On 2017 Sep 05, Kath Wright commented:

This paper has been added to the issg Search Filter Resource at https://sites.google.com/a/york.ac.uk/issg-search-filters-resource/adverse-events-filters

On 2016 Oct 19, Kelly Farrah commented:

Happy to hear that you found the analysis useful Michelle. Which filter did you end up choosing?

On 2016 Oct 14, Michelle Fiander commented:

Thanks very much for this analysis; am in the midst of a project and you have helped me determine which filter to use.

On 2016 Jul 14, Thomas E. Nichols commented:

This work has two unfortunate statements that can be misunderstood to mean that the findings apply to all "40,000" publications in the fMRI literature. The following two corrections will resolve this problem:

The last sentence of the Significance statement should read: “These results question the validity of a number of fMRI studies and may have a large impact on the interpretation of weakly significant neuroimaging results.”

The first sentence after the heading “The future of fMRI” should have read: “Due to lamentable archiving and data-sharing practices it is unlikely that problematic analyses can be redone.”

For more on this, see the blog entry "Bibliometrics of Cluster Inference" http://blogs.warwick.ac.uk/nichols/entry/bibliometrics_of_cluster/

On 2016 Nov 28, GERALD SMITH commented:

Comments on an article by Stahl et al., Genetics (2016)

In their article “Apparent epigenetic meiotic double-strand-break disparity in Saccharomyces cerevisiae: A meta-analysis,” STAHL et al. (2016) reanalyze published data on meiotic gene conversion patterns in S. cerevisiae. They infer that the pattern is subject to epigenetic influence and suggest that further experiments, which they are not able to conduct, should be done to test this idea. Relevant data showing this feature had been previously published in Genetics by the group of JÜRG KOHLI.

In their article “The mating-type-related bias of gene conversion in Schizosaccharomyces pombe” PARVANOV et al. (2008) assayed gene conversion at the ura4A hotspot during meiosis. They mated two pairs of strains that were isogenic except for the coupling relations of the mat and ura4A alleles, which are on separate chromosomes. Conversion was assayed after no mitotic divisions (zygotic meiosis) and after extensive (52 or 70) mitotic divisions (azygotic meiosis). The coupling relation made a highly significant (t-test, p < 0.001) 2-fold difference in zygotic meiosis, as also seen in extensive data in BAUR et al. (2005) but no significant difference in azygotic meiosis (ratios of 1.04 and 1.05 were observed). Thus, the coupling effect disappears during mitotic growth, fully consistent with the coupling effect on meiotic gene conversion pattern being epigenetic. BAUR et al. showed that the homolog entering the zygotic crosses in coupling with the h⁺ mating-type allele converted to wt about twice as frequently as did the homolog in coupling with h^-.

The reduction or abolition of the coupling effect by mutations that remove histone modifying enzymes (the acetyl transferases Gcn5 and Ada2 and the deactetylase Clr6), shown by PARVANOV et al., is also strong evidence that this effect is via chromatin structure (one definition of “epigenetic”).

It seems simplest to consider this epigenetic effect to be differential frequency of DSBs at the ura4A hotspot, depending on the coupling relation with the mating-type locus. Differential DSB frequency on the homologs was proposed by STAHL et al. for the effects on gene conversion patterns at HIS4 of S. cerevisiae reported by them and others. In both cases, however, the effect could be via differential repair of a DSB with the sister (resulting in no visible conversion, i.e., restoration) or with the homolog (potentially producing a convertant, either full or half). PARVANOV et al. discuss this possibility of differential repair, citing the differential binding of Swi5 DNA strand-exchange protein to the silent mat2 – mat3 loci in h^- and h⁺ strains (JIA et al. 2004). But this possibility seems at odds with swi2Δ having no significant effect on the coupling effect, yet Swi2 being required for the differential binding of Swi5. In addition, it is unclear that the differential binding of Swi5 to heterochromatin (mat2 – mat3) extends to euchromatin (i.e., at ura4A). Since ura4A has an exceptionally strong meiotic DSB hotspot associated with this transplacement (GREGAN et al. 2005) and since meiotic DSBs are affected by chromatin structure, it seems likely that the effect is via differential DSB frequency, as BAUR et al. and PARVANOV et al. also discuss.

Regardless of the molecular basis of the coupling effect, its disappearance upon mitotic growth of the diploid and its dependence on chromatin modifications establishes the effect as “epigenetic” by a commonly used definition. At the end of their Discussion, STAHL et al. say, “Of course, the conclusions and surmises of this paper are testable by the execution of properly controlled crosses, studies that we are unable to undertake ourselves.” These surmises had been tested years earlier by BAUR et al. and PARVANOV et al. and found to be true. It is unfortunate that their work was not cited by STAHL et al.

BAUR, M., E. HARTSUIKER, E. LEHMANN, K. LUDIN, P. Munz et al., 2005 The meiotic recombination hot spot ura4A in Schizosaccharomyces pombe. Genetics 169: 551-561.

GREGAN, J., P. K. RABITSCH, B. SAKEM, O. CSUTAK, V. LATYPOV et al., 2005 Novel genes required for meiotic chromosome segregation are identified by a high-throughput knockout screen in fission yeast. Current Biology 15: 1663-1669.

JIA, S., T. YAMADA and S. I. GREWAL, 2004 Heterochromatin regulates cell type-specific long-range chromatin interactions essential for directed recombination. Cell 119: 469-480.

PARVANOV, E., J. KOHLI and K. LUDIN, 2008 The mating-type-related bias of gene conversion in Schizosaccharomyces pombe. Genetics 180: 1859-1868.

STAHL, F. W., M. B. REHAN, H. M. FOSS and R. H. BORTS, 2016 Apparent epigenetic meiotic double-strand-break disparity in Saccharomyces cerevisiae: A meta-analysis. Genetics 204: 129-137.

On 2016 Sep 24, azita Hekmatdoost commented:

Comments on “No effects of oral vitamin D supplementation on non-alcoholic fatty liver disease in patients with type 2 diabetes: a randomized, double-blind, placebo-controlled trial”

Makan Cheraghpour1,a ; Alireza Ghaemi 2,a ; and Azita Hekmatdoost 3* 1 Nutrition and Metabolic Diseases Research Center, Ahvaz Jundishapur University of Medical Sciences, Ahvaz, IR Iran 2 Department of Basic Sciences and Nutrition, Health Sciences Research Center, School of Public Health, Mazandaran University of Medical Sciences, Sari, IR Iran 3 Department of Clinical Nutrition, Faculty of Nutrition and Food Technology, Shahid Beheshti University of Medical Sciences, Tehran, IR Iran *Corresponding Author: Azita Hekmatdoost, Department of Clinical Nutrition, Faculty of Nutrition and Food Technology, Shahid Beheshti University of Medical Sciences, Tehran, IR Iran a These two authors have equally contributed to this work.

Barchetta et al (1) recently reported that vitamin D supplementation for 24 weeks had no effect on non-alcoholic fatty liver disease in patients with type 2 diabetes. The results showed that consumption of high dose vitamin D lead to no significant changes in metabolic and cardiovascular parameters and hepatic steatosis in these patients. Considering the contradiction between these results and previous studies (2-9), we decided to point some overlooked points of this study despite the outstanding ones.<br> First, NAFLD is now one of the most common chronic diseases in the world and there is a direct link between the disease and other metabolic disorders such as obesity, type 2 diabetes and cardiovascular diseases (10). It seems that lifestyle plays an important role in the formation and progression of the disease, which shows wide variations due to changes in diet and lifestyle (11-12). In studies about patients with NAFLD evaluating the diet and its components such as energy, processed meat, total fat, trans/saturated -fatty acids, the type of carbohydrates is essential because any change in using them can be a potentially confounding factor in the results of this kind of studies (13-19). However, dietary intakes were not assessed in this study, and the study participants did not get any dietary recommendation at baseline to reduce this confounding factor. Second, many studies have shown that physical activity can lead to significant improvements in metabolic parameters and liver steatosis in patients with NAFLD (11). This confounding factor was dissembled in this study because it was not assessed during the study and there was no recommendation to the patients in this regard. Thirdly, sunlight is one of the most important sources of vitamin D in the human body, so that exposure to the sun can supply the daily requirement of vitamin D. There is no assessment of this variable in this study to overcome its effect as a confounding factor. Finally, we recommend making a revision of this study because vitamin D is a cheap and safe supplement and acceptable for most patients. Thus, vitamin D supplementation for treatment or prevention of metabolic diseases such as NAFLD may be useful for health and well-being of society. More researches are needed in this area. References 1. Barchetta I, Del Ben M, Angelico F, Di Martino M, Fraioli A, La Torre G, et al. No effects of oral vitamin D supplementation on non-alcoholic fatty liver disease in patients with type 2 diabetes: a randomized, double-blind, placebo-controlled trial. BMC Med. 2016;14:92. 2. Chung GE, Kim D, Kwak MS, Yang JI, Yim JY, Lim SH, et al. The serum vitamin D level is inversely correlated with nonalcoholic fatty liver disease. Clin Mol Hepatol. 2016 Mar;22(1):146-51. 3. Foroughi M, Maghsoudi Z, Askari G. The effect of vitamin D supplementation on blood sugar and different indices of insulin resistance in patients with non-alcoholic fatty liver disease (NAFLD). Iran J Nurs Midwifery Res. 2016 Jan-Feb;21(1):100-4. 4. Leung PS. The Potential Protective Action of Vitamin D in Hepatic Insulin Resistance and Pancreatic Islet Dysfunction in Type 2 Diabetes Mellitus. Nutrients. 2016 Mar;8(3):147. 5. Luger M, Kruschitz R, Kienbacher C, Traussnigg S, Langer FB, Schindler K, et al. Prevalence of Liver Fibrosis and its Association with Non-invasive Fibrosis and Metabolic Markers in Morbidly Obese Patients with Vitamin D Deficiency. Obes Surg. 2016 Mar 17. 6. Mohamed Ahmed A, Abdel Ghany M, Abdel Hakeem GL, Kamal A, Khattab R, Abdalla A, et al. Assessment of Vitamin D status in a group of Egyptian children with non alcoholic fatty liver disease (multicenter study). Nutr Metab (Lond). 2016;13:53. 7. Nelson JE, Roth CL, Wilson LA, Yates KP, Aouizerat B, Morgan-Stevenson V, et al. Vitamin D Deficiency Is Associated With Increased Risk of Non-alcoholic Steatohepatitis in Adults With Non-alcoholic Fatty Liver Disease: Possible Role for MAPK and NF-kappaB? Am J Gastroenterol. 2016 Jun;111(6):852-63. 8. Wang D, Lin H, Xia M, Aleteng Q, Li X, Ma H, et al. Vitamin D Levels Are Inversely Associated with Liver Fat Content and Risk of Non-Alcoholic Fatty Liver Disease in a Chinese Middle-Aged and Elderly Population: The Shanghai Changfeng Study. PLoS One. 2016;11(6):e0157515. 9. Zhai HL, Wang NJ, Han B, Li Q, Chen Y, Zhu CF, et al. Low vitamin D levels and non-alcoholic fatty liver disease, evidence for their independent association in men in East China: a cross-sectional study (Survey on Prevalence in East China for Metabolic Diseases and Risk Factors (SPECT-China)). Br J Nutr. 2016 Apr;115(8):1352-9. 10. Eslamparast T, Eghtesad S, Poustchi H, Hekmatdoost A. Recent advances in dietary supplementation, in treating non-alcoholic fatty liver disease. World journal of hepatology. 2015 Feb 27;7(2):204-12. 11. Ghaemi A, Taleban FA, Hekmatdoost A, Rafiei A, Hosseini V, Amiri Z, et al. How Much Weight Loss is Effective on Nonalcoholic Fatty Liver Disease? Hepat Mon. 2013;13(12):e15227. 12. Hekmatdoost A, Shamsipour A, Meibodi M, Gheibizadeh N, Eslamparast T, Poustchi H. Adherence to the Dietary Approaches to Stop Hypertension (DASH) and risk of Nonalcoholic Fatty Liver Disease. Int J Food Sci Nutr. 2016 Jul 19:1-6. 13. Eslamparast T, Poustchi H, Zamani F, Sharafkhah M, Malekzadeh R, Hekmatdoost A. Synbiotic supplementation in nonalcoholic fatty liver disease: a randomized, double-blind, placebo-controlled pilot study. Am J Clin Nutr. 2014 Mar;99(3):535-42. 14. Faghihzadeh F, Adibi P, Hekmatdoost A. The effects of resveratrol supplementation on cardiovascular risk factors in patients with non-alcoholic fatty liver disease: a randomised, double-blind, placebo-controlled study. Br J Nutr. 2015 Sep 14;114(5):796-803. 15. Faghihzadeh F, Adibi P, Rafiei R, Hekmatdoost A. Resveratrol supplementation improves inflammatory biomarkers in patients with nonalcoholic fatty liver disease. Nutr Res. 2014 Oct;34(10):837-43. 16. Rahimlou M, Yari Z, Hekmatdoost A, Alavian SM, Keshavarz SA. Ginger Supplementation in Nonalcoholic Fatty Liver Disease: A Randomized, Double-Blind, Placebo-Controlled Pilot Study. Hepat Mon. 2016 Jan;16(1):e34897. 17. Shavakhi A, Minakari M, Firouzian H, Assali R, Hekmatdoost A, Ferns G. Effect of a Probiotic and Metformin on Liver Aminotransferases in Non-alcoholic Steatohepatitis: A Double Blind Randomized Clinical Trial. Int J Prev Med. 2013 May;4(5):531-7. 18. Yari Z, Rahimlou M, Eslamparast T, Ebrahimi-Daryani N, Poustchi H, Hekmatdoost A. Flaxseed supplementation in non-alcoholic fatty liver disease: a pilot randomized, open labeled, controlled study. Int J Food Sci Nutr. 2016 Jun;67(4):461-9. 19. Askari F, Rashidkhani B, Hekmatdoost A. Cinnamon may have therapeutic benefits on lipid profile, liver enzymes, insulin resistance, and high-sensitivity C-reactive protein in nonalcoholic fatty liver disease patients. Nutr Res. 2014 Feb;34(2):143-8.

On 2016 Jul 05, Holger Schunemann commented:

The comment by Messori and colleagues puzzles me. Why would one search using the term "GRADE method"? GRADE has rarely, if ever, been referred to as a "method". It has typically been described as a system, approach, framework etc. Thus, what if Messory and colleagues would use a more appropriate (more sensitive) search including GRADE system, approach, GRADE framework or just GRADE? Without appropriate searching for information this comment seems not useful. Also, perhaps, when the purpose of the comment is clear, a citation based search would be helpful. GRADE articles have been cited over 20,000 times and there will probably be useful information from 100's of guidance documents that have been developed with GRADE and the cited GRADE publications (beginning in 2003).

On 2016 Jul 01, Andrea Messori commented:

Structured methods of analysis and reporting: a quick literature analysis

Sabrina Trippoli and Andrea Messori

HTA Unit, ESTAR, Regional Health Service, 50100 Firenze (Italy)

In the evaluation of therapeutic interventions, structured methods of analysis and reporting are increasingly being proposed (1-6). Among these, the GRADE method (4-6), firstly described in 2004, is the most widely recognised at international level. For example, Alonso-Coello and colleagues (7) have pointed out that the “more than 100 organisations globally, including the World Health Organization, the Cochrane Collaboration, and the National Institute for Health and Care Excellence now use or have adopted the principles of the GRADE system”. In the present comment, we report the results of a preliminary literature analysis that we conducted to explore the contents of the published articles dealing with the GRADE method. Our analysis was restricted to journals indexed by PubMed (www.pubmed.gov).

a) Search engine: PubMed

b) Search term: “GRADE method”

c) Date of the search: 1 July 2016

d) Extracted citations: N=71

e) No. of citations not pertinent with the search term (false positive): N=17

f) No. of citations pertinent with the search term: N=54

g) No. of citations the contents of which were restricted to a description of the GRADE method and/or the intention to use this method for future activities: N=12

h) No. of citations the contents of which were represented by an experience of application of the method along with the results of this application: N=42. Of these 42 papers, 32 used the GRADE method with the only purpose of assessing the quality of evidence of the clinical material included in a systematic review or a meta-analysis; the remaining 10 of these 42 papers applied the GRADE method to the development of clinical guidelines or recommendations.

References

1. Schnipper LE, Davidson NE, Wollins DS, et al: American Society of Clinical Oncology statement: A conceptual framework to assess the value of cancer treatment options. J Clin Oncol 2015;33:2563-2577.

2. Schnipper LE, Davidson NE, Wollins DS, et al: Updating the ASCO value framework: Revisions and reflections in response to comments received. J Clin Oncol 2016, doi: 10.1200/JCO.2016.68.251

3. Cherny NI, Sullivan R, Dafni U, et al: A standardised, generic, validated approach to stratify the magnitude of clinical benefit that can be anticipated from anti-cancer therapies: The European Society for Medical Oncology Magnitude of Clinical Benefit Scale (ESMO-MCBS). Ann Oncol 2015;26:1547-1573.

4. Atkins D, Best D, Briss PA, et al. GRADE Working Group. Grading quality of evidence and strength of recommendations.BMJ 2004;328:1490.

5. Guyatt GH, Oxman AD, Vist GE, et al. GRADE Working Group. GRADE: an emerging consensus on rating quality of evidence and strength of recommendations. BMJ 2008;336:924-6.

6. Guyatt G, Oxman AD, Akl EA, et al. GRADE guidelines: 1. Introduction-GRADE evidence profiles and summary of findings tables. J Clin Epidemiol2011;64:383-94.

7. Alonso-Coello P, Schünemann HJ, Moberg J, Brignardello-Petersen R, Akl EA, Davoli M, Treweek S, Mustafa RA, Rada G, Rosenbaum S, Morelli A, Guyatt GH, Oxman AD; GRADE Working Group. GRADE Evidence to Decision (EtD) frameworks: asystematic and transparent approach to making well informed healthcare choices. 1: Introduction. BMJ. 2016 Jun 28;353:i2016.

Address correspondence to: Dr.Andrea Messori, HTA Unit, ESTAR, Regional Health Service, 50100 Firenze (Italy)

On 2017 Dec 26, Kevin Kavanagh commented:

We have expressed concerns in a previous letter and PubMed Common’s posting regarding the article by Kelly, et al,(1) where the efficacy of the evaluated product may have been overstated.(2, 3) In the authors reply, data was presented which presents less than a 30% reduction(4) as opposed to a 42% which is stated in the article and advertised by the company.(1,5) To our knowledge the peer-review record has not been corrected. In addition, we have concerns regarding at least the appearance of an undeclared conflict-of-interest between one of the article’s authors, Connie Steed, and the company in question, DebMed.(6)

It has come to the authors’ attention that the editor in charge of adjudicating the above concerns may also have a conflict-of-interest with DebMed and with one of the authors of the manuscript in question. Significant concerns regarding the conflicts of interest of the Editor Elaine Larson have arisen because of the following associations:

• Co-Author with Connie Steed (one of the authors in the manuscript in question) and Paul Alpert (Vice President of Patient Safety Strategy for DebMed) in an article published in Feb 2011.(7). Conflicts-of-Interest stated the following “Elaine Larson has received research funding from Deb Worldwide Healthcare, Inc.”

• Co-Author with Paul Alpert (Vice-President of Patient Safety Strategy for DebMed) in an article published in Jan 2013.(8)

• Co-Author with Paul Alpert (Vice-President of Patient Safety Strategy for DebMed) in an article published in Feb 2014.(9)

• Connie Steed, RN is listed as the 2016 Secretary for the Association for Professionals in Infection Control and Epidemiology, Inc., which has as its official publication the American Journal of Infection Control(10) and provides this Journal as a benefit of their membership.(11)

We feel that because of the above, the appearance of a conflict of interest exists which may have clouded the decision making and inhibited the correction of the potential research integrity problems in the article in question.

References

(1) Kelly, J.W., Blackhurst, D., McAtee, W., and Steed, C. Electronic hand hygiene monitoring as a tool for reducing health care-associated methicillin-resistant Staphylococcus aureus infection. Am J Infect Control. 2016; 44: 956–95 Kelly JW, 2016

(2) Kavanagh KT, Saman DM. Comment Regarding: Electronic hand hygiene monitoring as a tool for reducing health care–associated methicillin-resistant Staphylococcus aureus infection. American Journal of infection Control. December 01 2016 http://www.ajicjournal.org/article/S0196-6553(16)30904-X/fulltext

(3) Kavanagh KT, Saman DM. Comment on PMID: 27908437: Response to Letter Regarding Manuscript “Electronic Hand Hygiene Monitoring as a Tool for Reducing Nosocomial Methicillin-resistant Staphylococcus aureus Infection” In: PubMed Commons [Internet]. Bethesda (MD): National Library of Medicine; 2016 Dec. 16. Available from: https://www.ncbi.nlm.nih.gov/pubmed/27908437#cm27908437_34333

(4) Kelly JW, Blackhurst D, McAtee W, Steed C. Response to Letter Regarding Manuscript "Electronic Hand Hygiene Monitoring as a Tool for Reducing Nosocomial Methicillin-resistant Staphylococcus aureus Infection". Am J Infect Control. 2016 Dec 1;44(12):1763. doi>: 10.1016/j.ajic.2016.08.009. http://www.ajicjournal.org/article/S0196-6553(16)30812-4/fulltext Kelly JW, 2016

(5) DebMed: Discover how one facility was able to reduce MRSA HAIs by up to 42%. Last accessed on Dec. 21, 2017 from http://info.debmed.com/mrsa-study-flyer

(6) Hospital Reduces MRSA Rates by 42% with electronic hand hygiene measurement. Infection Control Today. July 8, 2016. http://www.infectioncontroltoday.com/news/2016/07/hospital-reduces-mrsa-rates-by-42-with-electronic-hand-hygiene-measurement.aspx

(7) Connie Steed, MSN, RN, CIC J. William Kelly, MD Dawn Blackhurst, DrPH Sue Boeker, BSN, RN, CIC Thomas Diller, MD, MMM Paul Alper, BA Elaine Larson, RN, PhD, FAAN, CIC Hospital hand hygiene opportunities: Where and when (HOW2)? The HOW2 Benchmark Study. American Journal of Infection Control. Feb 2011 39(1):19-26. Steed C, 2011

(8) Buet A, Cohen B, Marine M, Scully F, Alper P, Simpser E, Saiman L, Larson E. Hand hygiene opportunities in pediatric extended care facilities. J Pediatr Nurs. 2013 Jan;28(1):72-6. doi: 10.1016/j.pedn.2012.04.010. Epub 2012 Jun 1. Buet A, 2013

(9) Conway LJ, Riley L, Saiman L, Cohen B, Alper P, Larson EL. Implementation and impact of an automated group monitoring and feedback system to promote hand hygiene among health care personnel. Jt Comm J Qual Patient Saf. 2014 Sep;40(9):408-17. Conway LJ, 2014

(10) American Journal of Infection Control Home Page. Accessed on Dec. 26, 2017 from https://www.journals.elsevier.com/ajic-american-journal-of-infection-control

(11) Association for Professionals in Infection Control and Epidemiology, Inc. Web Posting. Accessed on Dec. 26, 2017 from http://www.ajicjournal.org/article/S0196-6553(15)01270-5/pdf

Comment also posted on PubPeer

On 2017 Nov 30, Natalie Clairoux commented:

Free version of this article available after March 29, 2018 at https://papyrus.bib.umontreal.ca/xmlui/handle/1866/19235

On 2016 Jun 25, Christopher Southan commented:

A nicely detailed paper but it seems odd the structures were not deposited in PDB since the coordinates (460 pages!) are already published in WO2015200795. CC-885 is now entered into Guide to PHARMACOLOGY as ligand ID 9224 (live link pending in July release)

On 2016 Jun 30, Atanas G. Atanasov commented:

For broader view on the significance of natural products in drug discovery and development, you might also check:

http://dx.doi.org/10.1016/j.biotechadv.2015.08.001

(“Discovery and resupply of pharmacologically active plant-derived natural products: A review”)

On 2016 Jun 27, L. Miguel Martins commented:

We have a video abstract for this paper here: https://youtu.be/13oA5eiH-8s

On 2016 Oct 24, Sean Ekins commented:

THis work gets a mention alongside other machine learning efforts http://www.slideshare.net/ekinssean/using-machine-learning-models-based-on-phenotypic-data-to-discover-new

On 2016 Jul 10, Marios Kyriazis commented:

There is a fundamental issue which many people either forget or choose to ignore. The effort to reduce, reverse or postpone aging should not reflect our innate wish to 'live longer'.Instead it reflects a medical aim to reduce, eliminate or avoid age-related, chronic degeneration, which leads to dysfunction. It is not a matter of simply accepting the finitude of life, because this finitude is necessarily associated with chronic dysfunction and disease which would not be present if we find ways to avoid aging.

On 2016 Aug 26, Sharanbasappa Durg commented:

The treatment of low back pain (LBP) is challenging and guidelines recommend medications with proven benefits. Further, patients’ preference should be considered in the treatment of pain. Systematic reviews (mainly of randomized controlled trials [RCTs]), with or without meta-analysis, are generally considered to provide the key evidence in the practice of evidence-based medicine.

The systematic review and meta-analysis by Abdel Shaheed C, 2017 pooled all the available clinical evidence (of RCTs) on the use of muscle relaxants (Thiocolchicoside, Carisoprodol, Tizanidine, Eperisone, Pridinol, Flupirtine, Cyclobenzaprine) for LBP. Most of the included trials evaluated the efficacy and safety of muscle relaxants in acute LBP participants. The controls were mainly either placebo or nonsteroidal anti-inflammatory drugs (NSAIDs). The study authors could have tried some meta-analysis on important physiological outcomes. This systematic review concluded that muscle relaxants provide clinically significant pain relief for acute LBP.

Similar outcomes were observed in a systematic literature review on Eperisone for LBP by Bavage S, 2016, 2016. In this systematic review, the authors found that intervention with Eperisone may be effective in acute LBP patients with less adverse effects. Further, Eperisone also improved paraspinal blood flow in chronic LBP patients.

Both the systematic reviews, however, did not find any considerably support for the use of muscle relaxants in chronic LBP patients. Though, few RCTs evaluated the efficacy and safety of muscle relaxants in chronic LBP. Future research should emphasize more on finding the clinical evidence whether muscle relaxants have beneficial effects in patients with chronic LBP.

On 2016 Aug 26, Sharanbasappa Durg commented:

None

On 2016 Aug 25, Gerard Ridgway commented:

There is some very interesting discussion of this paper on AlzForum. In particular, Pieter Jelle Visser reports a strong correlation (0.8) between CSF Aβ1-42 and amyloid PET, and David Holtzman notes that CSF Aβ1-42 drops at or before detectable PiB positivity, and that PiB is in turn more sensitive than florbetapir. Another recent paper using ADNI data (Palmqvist S, 2016) also concludes that CSF Aβ1-42 "becomes abnormal in the earliest stages of Alzheimer's disease, before amyloid positron emission tomography and before neurodegeneration".

These results seem strongly discordant with Figure 3 in this paper, which shows florbetapir Aβ deposition occurring second (after vascular abnormalities) and becoming fully abnormal in established LOAD, but CSF Aβ1-42 abnormalities occurring last (out of 9 biomarkers), and reaching an abnormality level of only about 1/3. If this difference between amyloid PET and CSF Aβ1-42 results is considered implausible, then that could suggest a modelling problem that could also call into question the key finding of early vascular abnormalities.

On 2017 Nov 27, Eyal Shahar commented:

"The consistency thingamajig is a bundle of biases rolled into one. First, it is the assumption that effect‐modification is absent (which is strange by itself because effect modification plays a bizarre role in determinism.) Second, the claim that exposure needs to be “defined” either leads to thought bias or illustrates misunderstanding of information bias."

The consistency rule http://www.u.arizona.edu/~shahar/commentaries.html

On 2017 Jun 09, GERALD SMITH commented:

In Ma et al. (1), we isolated Schizosaccharomyces pombe ctp1 point mutations, which we interpreted to separate genetically two known meiotic activities that depend on Ctp1 for meiotic DNA break repair. A later paper by Jensen and Russell (2) claimed these activities are not genetically separable. We believe the disparity in interpretation stems largely from the use of meiotic cells in our studies but mitotic cells by Jensen and Russell. We maintain that in meiotic cells the activities are genetically separable.

During S. pombe meiosis, Rec12 (Spo11 homolog) makes DNA double-strand breaks (DSBs) and remains covalently linked to each 5’ end. The Mre11-Rad50-Nbs1 (MRN)-Ctp1 complex endonucleolytically removes Rec12 covalently linked to a short oligonucleotide (Rec12-oligo), an activity called “clipping.” The recessed 5’ end is then further digested, an activity called “resection,” to form a long 3’ single-stranded DNA tail that forms with intact DNA a joint DNA molecule to continue DSB repair. We concluded that most of the dozen ctp1 point mutants we studied retained nearly wild-type levels of resection but little clipping activity during meiosis. These conclusions were based on concordant genetic and physical analyses. Although we isolated these mutants based on a mitotic screen, we drew all of our conclusions from meiotic data.

In our physical assays for clipping, we found in wild-type cell extracts abundant Rec12-oligos, which were absent or barely detectable in ctp1 mutant extracts, either point mutant or complete deletion (ctp1Δ). Failure to clip off Rec12 leaves irreparable DSBs and consequently inviable spores; the ctp1 point mutants had 10- to 30,000-fold, and ctp1Δ 100,000-fold, reductions of viable spore yields compared to wild type. These results indicate that the ctp1 mutants have strongly reduced clipping activity.

To assay resection, we induced in meiotic cells a DSB at a well-defined site, using either the I-SceI or the I-PpoI homing endonuclease. Physical assays using Southern blots showed that resection of the DSB end proceeded as rapidly and extensively in the ctp1 point mutants as in wild type but slowly and to a much lesser extent in the ctp1Δ mutant. The homing endonucleases form DSBs without a covalently bound protein; I-SceI-dependent recombination thus requires resection but not clipping. In the ctp1 point mutants, the frequency of this recombination was equal to, or even twice as high as, that in ctp1+ cells, which was ~5 times higher than that in the ctp1Δ mutant. Thus, both physical and genetic assays indicate that resection is robust in the ctp1 point mutants.

In interpreting these results, it is important to consider the role of Exonuclease I (ExoI), which could potentially resect DSB ends and produce recombinants. The MRN complex blocks ExoI access to DSBs in meiotic cells, but the Ku complex blocks ExoI in mitotic cells. Thus, ExoI plays no apparent role in DSB repair in meiotic cells with an intact MRN complex; instead, MRN promotes access of Ctp1 to DSB ends. For example, in meiotic cells exoIΔ has no significant effect on I-SceI-dependent recombination, but ctp1Δ reduces it by a factor of ~5 (3). Conversely, in rad50Δ mutants ctp1Δ has no significant effect, but exoIΔ reduces recombination by a factor of ~4. As expected, the ctp1Δ exoIΔ double mutant is like ctp1Δ in rad50+ cells but like exoIΔ in rad50Δ mutants.

Jensen and Russell (2) assessed the mitotic activity of two of our ctp1 point mutants, along with ctp1+ and ctp1Δ, by analyzing the number and sizes of colonies formed on agar plates containing DNA damaging agents and spotted with 5-fold serial dilutions of cell cultures. Their results, like ours, showed that ctp1-6 and ctp1-25 are more DNA damage-resistant than the ctp1Δ mutant, indicating that the point mutants retain some activity. Removal of the Ku complex, by pku80Δ, suppressed these sensitivities but only if ExoI was present. Removal of ExoI enhanced the sensitivity to some agents (e.g., methyl methanesulfonate) but not, or only slightly, to others (e.g., ionizing radiation). In each of these various combinations, the point mutants were more resistant than the ctp1Δ mutant, confirming our results that the point mutants retain some activity. In nine out of ten cases, the ctp1-6 exoIΔ and ctp1-25 exoIΔ mutants were more resistant than ctp1Δ exoIΔ, which was completely sensitive to the agents tested. This result shows that the ctp1 point mutants retain an activity that can be supplied by ExoI, which we take to be resection.

Jensen and Russell proposed that the ctp1 point mutations reduce, but do not abolish, a single activity. They further proposed that this residual activity is sufficient to repair a single DSB per cell (as in the I-SceI and I-PpoI experiments we reported) but not multiple DSBs per cell [as in the experiments with wild-type Rec12, which makes about 60 DSBs per meiotic cell (4)]. This proposal is hard to reconcile with our physical assays of clipping and resection noted above. It is not clear to us how a single Ctp1 activity could be altered, in either KM or kcat, to resect one DSB in a cell with wild-type kinetics but not clip Rec12 off 60 DSBs in a cell if resection and clipping result from the same activity, since both processes take about the same amount of time. Rather, we think the mutant proteins have greater reductions of clipping activity than of resection activity. Reduction of the number of Ctp1 molecules per cell, from 60 or more to about 1, could account for our results, but we consider this an unlikely explanation for the many mutants we studied. Instead, we think our mutants have retained nearly wild-type levels of resection but have strongly reduced levels of clipping, in meiotic cells. Whether the active sites for these two activities are in Ctp1, the MRN complex, or both is not addressed by our experiments. Without tests of a very large number of Ctp1 mutants under many conditions, we think the conclusion that the two activities are not genetically separable is unwarranted.

Lijuan Ma, Neta Milman, Mridula Nambiar, and Gerald R. Smith

References:

1. Ma, L., Milman, N., Nambiar, M. and Smith, G.R. (2015) Two separable functions of Ctp1 in the early steps of meiotic DNA double-strand break repair. Nucleic Acids Res., 43, 7349-7359.

2. Jensen, K.L. and Russell, P. (2016) Ctp1-dependent clipping and resection of DNA double-strand breaks by Mre11 endonuclease complex are not genetically separable. Nucleic Acids Res., 44, 8241-8249.

3. Farah, J.A., Cromie, G.A. and Smith, G.R. (2009) Ctp1 and Exonuclease 1, alternative nucleases regulated by the MRN complex, are required for efficient meiotic DNA repair and recombination. Proc. Natl. Acad. Sci. USA, 106, 9356-9361.

4. Fowler, K.R., Sasaki, M., Milman, N., Keeney, S. and Smith, G.R. (2014) Evolutionarily diverse determinants of meiotic DNA break and recombination landscapes across the genome. Genome Res., 24, 1650-1664.

On 2017 Sep 20, Jim Woodgett commented:

Since GSK-3alpha is equally inhibited by lithium, the power of this study may have been increased if phosphorylation of Serine 21 of the alpha isoform had been measured too.

On 2016 Jul 21, David Keller commented:

Aluminum exposure raised dementia risk by 71% in meta-analysis. 44% PPI dementia risk needs correction for aluminum-containing antacids!

Dietary aluminum ingestion is theorized to be neurotoxic and play a causative role in the onset and progression of dementia. [1-3] A recent meta-analysis showed that individuals chronically exposed to aluminum were 71% more likely to develop Alzheimer disease (odds ratio, 1.71; 95% CI, 1.35-2.18).[4] Many strong antacids contain aluminum hydroxide and are often taken for years by patients with peptic ulcer disease or gastroesophageal reflux before they are prescribed proton pump inhibitors, and concurrent with their use. Gomm and colleagues [5] did not correct for the use of aluminum-containing antacids when calculating the association of dementia with proton pump inhibitor use. How much of their observed association of proton pump inhibitor use with dementia is actually due to long-term ingestion of aluminum antacids, either currently or in the past?

References

1: Bhattacharjee S, Zhao Y, Hill JM, Percy ME, Lukiw WJ. Aluminum and its potential contribution to Alzheimer's disease (AD). Front Aging Neurosci. 2014 Apr 8;6:62. doi: 10.3389/fnagi.2014.00062. eCollection 2014. PubMed PMID:24782759; PubMed Central PMCID: PMC3986683.

2: Rodella LF, Ricci F, Borsani E, Stacchiotti A, Foglio E, Favero G, Rezzani R, Mariani C, Bianchi R. Aluminium exposure induces Alzheimer's disease-like histopathological alterations in mouse brain. Histol Histopathol. 2008 Apr;23(4):433-9. PubMed PMID: 18228200.

3: Exley C. What is the risk of aluminium as a neurotoxin? Expert Rev Neurother. 2014 Jun;14(6):589-91. doi: 10.1586/14737175.2014.915745. Epub 2014 Apr 30. PubMed PMID: 24779346.

4: Wang Z, Wei X, Yang J, Suo J, Chen J, Liu X, Zhao X. Chronic exposure to aluminum and risk of Alzheimer's disease: A meta-analysis. Neurosci Lett. 2016 Jan 1;610:200-6. doi:10.1016/j.neulet.2015.11.014. Epub 2015 Nov 27. PubMed PMID: 26592479.

5: Gomm W, von Holt K, Thomé F, et al. Association of proton pump inhibitors with risk of dementia: a pharmacoepidemiological claims data analysis [published online February 15, 2016]. JAMA Neurol. doi:10.1001/jamaneurol.2015.4791.

On 2016 Aug 03, Murat Büyükşekerci commented:

Dear Sir In Page 26, under title "5.1 Pain Chronification", it is written as 'For example, neurokinin has been shown to both decrease inflammatory pain and joint cartilage destruction in rats [176, 177]. According to referenced atricles it should be like this '..NEUROKİNİN RECEPTOR ANTAGONİSTS.." not neurokinin. Thanks.

On 2016 Aug 02, Murat Büyükşekerci commented:

In page 13 under heading 3.8 Glutamate it is written as "They showed that alpha-2 antagonists inhibit the auto-phosphorylation of CaMKII, proposing that reduced CaMKII activity may lead to dephosphorylation of NMDA and AMPA glutamate receptors and a corresponding decrease in nociceptive transmission [77]." However, as we read the referenced article* clonidin ,an alpha-2 agonist, did inhibit the auto-phosphorylation of CaMKII but not any alpha-2 antagonists. I would like to point this misinterpret. Thank you for considering.

*Wang XT, Lian X, Xu YM, et al. Alpha2 noradrenergic receptor suppressed CaMKII signaling in spinal dorsal horn of mice with inflammatory pain. Eur J Pharmacol 2014;724:16-23.

On 2017 Dec 10, Ricardo Belda commented:

Any subclinical leaks revealed by the tomography? Congrats

On 2018 Jan 12, Stefan Tino Kulnik commented:

Further to my comment from 13 October 2017:

In June 2017, we approached Journal of Physiotherapy and submitted a commentary, in which we pointed out the error in this meta-analysis and that the authors’ conclusion with respect to the impact of respiratory muscle training on respiratory complications is therefore unfounded. Unfortunately our commentary was rejected, and so we were denied the opportunity of entering a scientific exchange with the authors within the pages of the journal.

The journal did acknowledge the data extraction error we pointed out and promised a correction, but a correction has not been published to date.

It may be regarded as rather unfortunate that this systematic review and meta-analysis (a study design that many colleagues in clinical practice will view as highest level evidence) presents a strong clinical message in favour of implementing respiratory muscle training for the prevention of respiratory complications, based on an erroneous meta-analysis.

Burden of treatment and opportunity cost to stroke survivors should not be underestimated, and it is important to focus clinical resources on the most meaningful rehabilitation activities based on best evidence.

For members of the research community and colleagues in clinical practice who may be interested, I have uploaded the content of our rejected commentary on my ResearchGate page https://tinyurl.com/yb3wxmkf. In this we also present a re-calculated meta-analysis using Peto odds ratio, which is a more appropriate and statistically more powerful model of meta-analysis when events are rare, to demonstrate that even with this statistically more powerful method the meta-analysis still fails to reach statistical significance of the overall effect.

On 2017 Oct 13, Stefan Tino Kulnik commented:

I write to highlight an error in this systematic review and meta-analysis of respiratory muscle training after stroke. The authors present a meta-analysis, in which data from two randomised controlled trials of respiratory muscle training in stroke were pooled (Figure 6). Respiratory muscle training is reported to result in a statistically significant risk reduction for the outcome respiratory complications (overall risk ratio 0.38, 95%CI 0.15 to 0.96).

It is this journal’s policy to publish simplified forest plots in the main article, and to provide detailed forest plots in an online supplement. It is therefore not immediately evident that in this meta-analysis there has been a data extraction error from one of the included studies.

The detailed forest plot for this analysis (Figure 7 in the online supplement) shows that for meta-analysis two intervention groups in the study by Kulnik ST, 2015 were combined to a total of n=53. The number of respiratory complications in this combined group is given as n=5, but in fact it was n=9. The correct overall risk ratio in meta-analysis (Mantel-Haenszel random effects model in RevMan, Version 5.3, 2014) is therefore 0.49 (95%CI 0.09 to 2.65). While this re-calculated point estimate still favours the intervention, it is no longer statistically significant.

This demonstrates how in studies such as these, where sample sizes are small and events are rare, small inaccuracies can have a considerable influence on statistical results.

Further studies are required to demonstrate a statistically significant effect of respiratory muscle training on respiratory complications after stroke. There is a good theoretical rationale why respiratory muscle training might reduce respiratory complications after stroke, but definitive empirical evidence is lacking at the moment.

On 2016 Sep 02, monique dontenwill commented:

In this publication it is not clear if the authors address the ITGA5 integrin or the ITGAV integrin which are quite different integrins. Alpha5 integrin makes an heterodimer with beta1 integrin to form the fibronectin receptor alpha5beta1 and alphav integrin associates with beta3 integrin to form the alphavbeta3 integrin which recognizes fibronectin and vitronectin. Although in the results part it is question of alpha5 integrin,in the discussion only references about alphavbeta3 integrin are given.

On 2016 Nov 28, Lydia Maniatis commented:

Please see comments on PubPeer.

On 2016 Aug 01, Joaquim Radua commented:

Re: the previous comment, I think there may be some unfortunate confusion. Raw p-values of current voxelwise meta-analyses have not the same meaning as usual p-values because they are not derived from the usual null hypothesis (“there are no differences between groups”), but from another null hypothesis (“all voxels show the same difference between groups”). Thus, up to the moment one of the only ways to "approximately" know if the results of a voxelwise meta-analysis are neither too liberal nor too conservative is to compare them with the results of a mega-analysis of the same data, and that's what it was done.

On 2016 Jul 20, Christopher Tench commented:

Here the authors have swapped a method that employs disciplined control of the type 1 error rate (FDR) for a method (SDM) that employs no disciplined control in order to demonstrate there are regions of true positive atrophy in narcolepsy. It does not, however, provide any evidence of this. Arbitrary p-value thresholds do not work in neuroscience. They most certainly do not make a meta-analysis, which demands rigorous statistics. There is no evidence of consistent reporting of regional GM atrophy from this study,

On 2016 Jul 21, Jacob H. Hanna commented:

In this elegant review, Wu and Belmonte discuss in detail (Figure 2 and page 1576 in this manuscript) experiments conducted by Theunissen et al. Cell Stem Cell 2014 Theunissen TW, 2014 claiming complete failure to detect human naïve PSC derived cell integration in chimeric mouse embryos obtained following microinjection into mouse blastocysts, as was reported for the first time by our group (Gafni et al. Nature 2013). However, in this review the authors failed to discuss that among different caveats, imaging and cell detection methods applied by Theunissen et al. Cell Stem Cell 2014 were (and still) not at par with those applied by Gafni et al. Nature 2013.

Regardless, we find it important to alert the readers that Theunissen and Jaenisch have now revised (de facto, retracted) their previous negative results, and are able to detect naïve human PSC derived cells in mouse embryos at more than 0.5-2% of embryos obtained (Theunissen et al. Cell Stem Cell 2016 - Figure 7) Theunissen TW, 2016 < http://www.cell.com/cell-stem-cell/fulltext/S1934-5909(16)30161-8 >. They now also apply GFP and RFP flourescence detection and genomic PCR based assays, which were applied by the same group to elegantly claim contribution of human neural crest cells into mouse embryos (albeit at low efficiency (Cohen et al. PNAS 2016 Cohen MA, 2016).

While the authors of the latter recent paper avoided conducting advanced imaging and/or histology sectioning on such obtained embryos, we also note that the 0.5-2% reported efficiency is remarkable considering that the 5i/LA (or 4i/LA) naïve human cells used lack epigenetic imprinting (due to aberrant loss of DNMT1 protein that is not seen in mouse naive ESCs!! http://imgur.com/M6FeaTs ) and are chromosomally abnormal. The latter features are well known inhibitors for chimera formation even when attempting to conduct same species chimera assay with mouse naïve PSCs.

Jacob (Yaqub) Hanna M.D. Ph.D.

Department of Molecular Genetics (Mayer Bldg. Rm.005)

Weizmann Institute of Science | 234 Herzl St, Rehovot 7610001, Israel

Email: jacob.hanna at weizmann.ac.il

Lab website: http://hannalabweb.weizmann.ac.il/

Twitter: @Jacob_Hanna

On 2016 Jul 14, Jacob H. Hanna commented:

None

On 2016 Aug 11, David C. Norris commented:

This Notice addresses "incorrect confidence intervals and a P value in 2 tables", errors that "were discovered in the course of rechecking the [statistical analysis] code in conjunction with a secondary analysis." My understanding (based on a 1/6/2016 personal communication from a member of the Kessler team) is that said "secondary analysis" would in fact be a reanalysis by myself and Andrew Wilson, which at the time of this Notice was published on F1000Research, and has since completed post-publication peer review and PubMed indexing.¹

Although the Kessler team's discovery of these programming errors does illustrate one benefit of the increased scrutiny a reanalysis engenders generally, it should be understood that this Retraction and Replacement is merely incidental to our reanalysis. In particular, this Retraction and Replacement does not address the original work's² nontransparent application of a dubious PTSD outcome imputation procedure which our reanalysis exposed. It is hoped that some comment on this substantive question will be forthcoming from the original authors, either here on PubMed Commons or through any of several mechanisms^3,4 provided by the F1000Research platform.

1] Norris DC, 2016

2] Kessler RC, 2014

3] F1000Research Policy for Comments on Articles

4] F1000Research - Preparing a Correspondence Article

On 2016 Jun 25, John D. Scott commented:

Response to Moore et al.

John D. Scott, B.Sc. (Agr.), M.Sc.

June 23, 2016

Re: Moore A, Nelson C, Molins C, Mead P, Schriefer M (2016) Current guidelines, common clinical pitfalls, and future direction for laboratory diagnosis of Lyme disease, United States. Emerg Infect Dis 22. doi 10.3201/eid2207.151694

The two-tiered Lyme disease serology test has failed countless patients, including my wife and me. We both have definitive proof of Lyme disease, and yet we have never tested positive using conventional two-tiered Lyme serology testing. We are culture-positive, PCR-positive, and show positivity for anti-Borrelia burgdorferi fluorescent stain on body fluids.

Using circular reasoning to tout the two-tiered Lyme disease serology test is unscientific. This spurious methodology is nothing more than stacking the deck before the experiment begins. Using only seropositive patients to show seropositivity is anti-science and highly flawed. In reality, the two-tiered system fails Lyme disease patients time and time again. When researchers flaunt a screening test that seldom works, it puts the populace at risk.

On 2016 Jun 18, Raphael Stricker commented:

Circular Reasoning in CDC Lyme Disease Test Review

Raphael B. Stricker, MD; Lorraine Johnson, JD, MBA

Previous studies have shown that commercial two-tier serological testing has a sensitivity of about 46% in later-stage Lyme disease in the USA [1]. Commercial two-tier Lyme testing in Europe demonstrates the same poor test sensitivity [2]. The Table in the latest Centers for Disease Control and Prevention (CDC) review by Moore et al. cites three studies allegedly showing that two-tier Lyme testing in later-stage (“non-cutaneous”) Lyme disease has a sensitivity of 87-96% [3]. These numbers will undoubtedly be used to support two-tier testing as a valid diagnostic tool for Lyme disease. Therefore it is important to understand the circular reasoning that produced these inflated and misleading numbers.

Analysis of the three studies cited in the CDC review reveals the following:

+1. Branda et al [4]: Two-tier Lyme test sensitivity 87% (55 patients). The Methods section of this article contains the following language: "All patients categorized as having Lyme disease met the CDC surveillance criteria for the diagnosis.” The reference for this statement [5] contains the CDC surveillance criteria for the diagnosis of Lyme disease. The portion of the CDC surveillance criteria relevant for later Lyme disease is set forth below.

Clinical case definition:

1. Erythema migrans, or
2. At least one late manifestation, as defined below, and laboratory confirmation of infection (emphasis added).

Laboratory criteria for diagnosis:

1. Isolation of Borrelia burgdorferi from clinical specimen, or
2. Demonstration of diagnostic levels of IgM and IgG antibodies to the spirochete in serum or CSF, or
3. Significant change in IgM or IgG antibody response to B. burgdorferi in paired acute- and convalescent-phase serum samples.

This surveillance case definition was developed for national reporting of Lyme disease; it is NOT appropriate for clinical diagnosis (emphasis added).

Comment: Although the Branda et al. study does not say how many later-stage Lyme patients were culture-positive, presumably most were included based on positive serology. Patients who had positive serology as part of the study entry criteria would be expected to have positive serology on the same outcome measure. Circular reasoning.

+2. Molins et al [6]: Two-tier Lyme test sensitivity 96% (46 patients). The Methods section of this article contains the following language: "Lyme disease serology or results from two-tiered testing did not play a role in patient enrollment except for inclusion of late-stage Lyme arthritis patients (emphasis added).”

Comment: Once again, patients with later-stage Lyme disease had to have positive serology in order to be included in the study, and then they had positive serology. Circular reasoning.

+3. Wormser et al [7]: Two-tier Lyme test sensitivity 94% (142 patients). This study was a cost analysis article based on another study [8] that contains the following language: "Lyme arthritis was defined as the presence of joint swelling that was clinically compatible with Lyme arthritis in conjunction with serologic evidence of borrelial infection demonstrated by at least a positive WCS ELISA (emphasis added).”

Comment: Once again, patients with later-stage Lyme disease had to have positive serology in order to be included in the study, and then they had positive serology. Circular reasoning.

Conclusions: Based on circular reasoning, the latest CDC analysis perpetuates the myth that two-tier testing is sensitive for later-stage Lyme disease. The comment in the CDC surveillance guidelines that this testing is NOT appropriate for clinical diagnosis is being ignored by the CDC.

References

[1] Stricker RB, Johnson L. Lyme disease diagnosis and treatment: Lessons from the AIDS epidemic. Minerva Med. 2010;101:419–25.

[2] Ang CW, Notermans DW, Hommes M, Simoons-Smit AM, Herremans T. Large differences between test strategies for the detection of anti-Borrelia antibodies are revealed by comparing eight ELISAs and five immunoblots. Eur J Clin Microbiol Infect Dis. 2011;30:1027-32.

[3] Moore A, Nelson C, Molins C, Mead P, Schriefer M. Current guidelines, common clinical pitfalls, and future directions for laboratory diagnosis of Lyme disease, United States. Emerg Infect Dis. 2016 Jul;22(7). doi: 10.3201/eid2207.151694.

[4] Branda JA, Linskey K, Kim YA, Steere AC, Ferraro MJ. Two-tiered antibody testing for Lyme disease with use of 2 enzyme immunoassays, a whole-cell sonicate enzyme immunoassay fol¬lowed by a VlsE C6 peptide enzyme immunoassay. Clin Infect Dis. 2011;53:541–7.

[5] Wharton M, Chorba TL, Vogt RL, Morse DL, Buehler JW. Case definitions for public health surveillance. MMWR Recomm Rep 1990; 39:1–43.

[6] Molins CR, Sexton C, Young JW, Ashton LV, Pappert R, Beard CB, et al. Collection and characterization of samples for establishment of a serum repository for Lyme disease diagnostic test development and evaluation. J Clin Microbiol. 2014;52:3755–62.

[7] Wormser GP, Levin A, Soman S, Adenikinju O, Longo MV, Branda JA. Comparative cost-effectiveness of two-tiered testing strategies for serodiagnosis of Lyme disease with noncutaneous manifestations. J Clin Microbiol. 2013;51:4045–9.

[8] Wormser GP, Schriefer M, Aguero-Rosenfeld ME, Levin A, Steere AC, Nadelman RB, et al. Single-tier testing with the C6 peptide ELISA kit compared with two-tier testing for Lyme disease. Diagn Microbiol Infect Dis. 2013;75:9–15.

Disclosure: RBS and LJ are members of the International Lyme and Associated Diseases Society (ILADS) and directors of LymeDisease.org. They have no financial or other conflicts to declare.

On 2016 Jun 18, Dirk Lachenmeier commented:

Thank you for the interesting report! Regarding the compounds responsible for allergic contact dermatitis, I believe that wormwood does not contain alcohol per se (this is probably a mismatch with the alcoholic beverage absinthe, which may contain Artemisia absinthium as ingredient). However, wormwood as many other Asteraceae plants contains sequiterpene lactones, which are known to cause such reactions from other species in the family, see e.g. https://www.ncbi.nlm.nih.gov/pubmed/12793186.

On 2016 Jul 07, GianCarlo Panzica commented:

More comments are in a previous article Slama R, 2016

and in a letter submitted after the publication of the decision of the European Commission Kortenkamp A, 2016

On 2016 Jul 22, Christopher Tench commented:

Excellent. The issue with the bug was that there was no FWER control, so without the test you have performed there is no way to know if there are any truly positive results. But now you have confirmed your study. Thanks.

On 2016 Jun 24, Maddalena Boccia commented:

We thank Christopher Tench for his comment following which we have re-run the analysis with GingerALE 2.3.6 where bug in Cluster level inference has been fixed. We are sorry for this but the paper has been accepted before the recognition of the so-mentioned bug. Anyway, we are glad to announce that the results are not changed at all, demonstrating that there is no actual false positive results but just the risk of false positive results, which is, together with the risk of false negative results, the two unavoidable scientific risks.

On 2016 Jun 19, Christopher Tench commented:

The version of GingerALE used (2.3.5) has an implementation issue that produces false positive results. This was fixed at 2.3.6.

On 2017 Aug 24, Serina Stretton commented:

Choi et al’s commentary, rightly condemns the practice of ghost writing in the peer-reviewed literature. Ghost writing (undisclosed contributions from individuals who DO NOT meet authorship criteria) and ghost authoring (undisclosed contributions from individuals who DO meet authorship criteria) are unethical practices and should be eradicated [1,2]. Here we address several of Choi et al’s assertions about the roles and responsibilities of professional medical writers (PMWs) and authors, and provide evidence of how PMWs can help deliver timely and accurate dissemination of clinical trial data.

As acknowledged by Choi et al and multiple editor organizations, including the International Committee for Medical Journal Editors (ICMJE) [1], the Council for Scientific Editors (CSE) [3], and the World Association of Medical Editors (WAME) [4], PMWs (individuals who do not meet authorship criteria and who declare their involvement in the acknowledgements) have a legitimate and valuable role in assisting authors disclose findings from clinical trials in the peer-reviewed literature. Publications involving PMWs are of higher quality compared with publications not involving PMWs or compared with publications that are not funded by industry; they can be more rapidly accepted through the peer-review process [5], more consistently meet the requirements set by international reporting guidelines [6, 7], contain significantly fewer non-prespecified outcomes [8], and are less likely to be retracted due to misconduct [9]. These outcomes are the result of authors working with PMWs who receive mandatory training on ethical publication practices and international reporting requirements from their employers and industry funders [10-12].

Choi et al put forward the scenario whereby authors play a seemingly passive role in the development of peer-reviewed manuscripts funded by the pharmaceutical industry. At worst, Choi et al assert that authors do not have access to raw data, may never have seen their publication before submission, and that industry-funded publications involving medical writers are riddled with embedded marketing messages. These assertions appear to absolve authors from any responsibility or accountability that they have as authors [1, 13]. Earlier this year, the American Medical Writers Association (AMWA), the European Medical Writers Association (EMWA), and the International Society for Medical Publication Professionals (ISMPP) released a joint position statement outlining the respective roles of authors and PMWs [14]. As required by the ICMJE [1] and upheld by the AMWA-EMWA-ISMPP joint position statement, authors must provide early intellectual input to a publication, be involved in the drafting, approve the final version for publication, and agree to be accountable for all aspects of the work. These last two requirements challenge Choi et al’s assertion that authors have no control over the content of their publications. Indeed, when working with PMWs, the PMW’s roles are to assist authors disclose their findings in a timely, ethical, and accurate manner, and to ensure that authors and sponsors are aware of their obligations, that author contributions during development of the manuscript are documented, and that the writer’s and sponsor’s involvement and funding are disclosed transparently and appropriately [12, 14]. In these ways, the PMW serves as a “gatekeeper” of compliance with widely-accepted standards of authorship.

We caution against conflating “ghost authorship” with “ghost writing”. Choi et al state that despite increased awareness of the need to avoid the unethical practice of ghostwriting, the prevalence remains high. In support of this, the authors cite Wislar et al’s survey of honorary or ghost authorship from 2008 [15], which showed that an individual who merited authorship was excluded from the author byline in 7.9% of articles. However, the prevalence of ghostwriting (an unnamed individual who participated in the writing) in this survey was far lower at 0.2%. In addition, findings from a systematic review of the literature suggest that the reported prevalence of ghostwriting in the medical literature can vary, but is on the decrease [16].

Choi et al finish by calling for a ban on “any manuscript that is discovered to be written by people other than the named authors”. We certainly agree if the assistance provided by other people is not disclosed transparently within the manuscript. However, we disagree that a ban on ethically conducted and appropriately acknowledged PMW assistance is warranted. We strongly urge authors and sponsors to select and work with PMWs on the basis of a proven track record and commitment to ethical and transparent publication practices. In addition, we urge authors to become familiar with reporting guidelines and be aware of, and fully comply with their obligations and roles as authors.

The Global Alliance of Publication Professionals (www.gappteam.org)

Serina Stretton, ProScribe – Envision Pharma Group, Sydney, NSW, Australia; Jackie Marchington, Caudex – McCann Complete Medical Ltd, Oxford, UK; Cindy W. Hamilton Virginia Commonwealth University School of Pharmacy, Richmond; Hamilton House Medical and Scientific Communications, Virginia Beach, VA, USA; Art Gertel, MedSciCom, LLC, Lebanon, NJ, USA; Julia Donnelly, Julia Donnelly Solutions Ltd, Ashbourne, UK.

GAPP is a group of independent individuals who volunteer their time and receive no funding (other than website hosting fees from the International Society for Medical Publication Professionals). All GAPP members have held, or do hold, leadership positions at associations representing professional medical writers (eg, AMWA, EMWA, DIA, ISMPP, ARCS), but do not speak on behalf of those organisations. GAPP members have, or do provide, professional medical writing services to not-for-profit and for-profit clients.

REFERENCES [1] www.icmje.org/recommendations/browse/roles-and-responsibilities/defining-the-role-of-authors-and-contributors.html; 2016 [accessed 08.06.17] [2] Gøtzsche PC et al. PLoS Med 2009;6:e23. [3] Council of Science Editors. White Paper on Publication Ethics - Council of Science Editors, http://www.councilscienceeditors.org/resource-library/editorial-policies/white-paper-on-publication-ethics/; [accessed 08.17.17]. [4] World Association of Medical Editors. Policy Statement: Ghost writing initiated by commercial companies, http://www.wame.org/about/policy-statements#Ghost Writing; 2005 [accessed 08.17.17]. [5] Bailey, M. AMWA J 2011;26(4):147-152 [6] Gattrell W et al. BMJ Open. 2016;6:e010329 [7] Jacobs A. Write Stuff 2010;19(3):196-200 [8] Gattrell W et al. ISMPP EU Annual Meeting 2017 [9] Woolley KL et al. Curr Med Res Opin 2011;27(6)1175-82 [10] www.ismpp.org/ismpp-code-of-ethics [accessed 08.06.17] [11] www.amwa.org/page/Code_of_Ethics [accessed 08.06.17] [12] Wager E et al. BMJ Open. 2014;4(4):e004780 [13] Battisti WP et al. Ann Intern Med. 2015;163(6):461-4 [14] www.ismpp.org/assets/docs/Inititives/amwa-emwa-ismpp joint position statement on the role of professional medical writers_january 2017.pdf 2017 [accessed 08.06.17] [15] Wislar JS et al. BMJ 2011;343:d6128.4-7 [16] Stretton S. BMJ Open 2014;4(7): e004777.

On 2016 Aug 01, David Keller commented:

A Hybrid Non-Invasive Colon Cancer Screening Strategy Lowers Cost/Benefit With Medicare Coverage

Many patients prefer to avoid invasive procedures and radiation exposure when screening for colon cancer. Non-invasive fecal testing fits these preferences, and can achieve results nearly as beneficial as colonoscopy every 10 years, according to CISNET (the Cancer Intervention and Surveillance Modeling Network) model outcomes displayed in Figure 3 of the 2016 USPSTF Recommendation Statement [1]. Colonoscopy-based screening yields the highest benefit, with an estimated 270 life-years gained per 1000 persons screened, closely followed by non-invasive Multi-Target FIT-DNA ("ColoGuard") testing every year with 261 life-years gained. The next-best non-invasive no-radiation strategy is annual testing for occult fecal blood using either immunochemical testing (FIT) or high-sensitivity guaiac (HSg-FOBT), which gain 244 and 247 life-years, respectively, followed by FIT-DNA performed once every 3 years, which gains only 226 life-years per thousand screened, about 15% less benefit than gained with annual FIT-DNA screening.

Partly due to the high cost of FIT-DNA testing, up to $649 per test [2], Medicare covers it only once per 3 years [2]. Medicare beneficiaries who are not willing to pay over $1200 out-of-pocket for the additional two non-covered test kits required for annual FIT-DNA screening may wish to consider an alternative strategy not discussed by CISNET: FIT-DNA testing every 3 years, plus annual FIT testing in the off-years. This "hybrid" combination should yield a benefit larger than annual FIT testing alone but smaller than annual FIT-DNA testing, putting it in the range of 244 to 261 life-years. Weighted interpolation using 2/3 times the FIT-alone benefit plus 1/3 times the FIT-DNA benefit yields an estimated benefit of 251 life-years per thousand screened, which is about 91 days of life per person screened.

It is uncertain whether the cost of the two annual FIT tests would be covered by Medicare for beneficiaries during their 3-year waiting period for their next FIT-DNA test. If not, the retail price of two FIT kits is about $30 [3], probably acceptable to most beneficiaries. Harms of hybrid every-3-year FIT-DNA screening plus FIT screening in the off-years should be larger than for annual FIT testing, but less than for annual FIT-DNA testing, because FIT is significantly more specific than FIT-DNA, 96.4% versus 89.8% respectively per test [4]. The harms of fecal screening are complications of colonoscopy triggered by positive screening test results, estimated at 12 GI or CV events for annual FIT-DNA, 10 events for annual FIT, [1], with an interpolated estimate of about 10.7 events for the hybrid strategy (all harms are expressed in events per 1000 persons screened).

References

1: US Preventive Services Task Force. Screening for Colorectal Cancer: US Preventive Services Task Force Recommendation Statement. JAMA. 2016 Jun 21;315(23):2564-75. doi:10.1001/jama.2016.5989. PubMed PMID: 27304597. See Figure 3 on page 2569.

2: ColoGuard website, accessed on 7/2/2016. http://www.cologuardtest.com/what-to-expect-with-cologuard/faq/cologuard-cost-how-much-is-cologuard and, Medicare official website, accessed on 7/2/2016. https://www.medicare.gov/coverage/colorectal-cancer-screenings.html

3: Pinnacle Labs website Fecal Immunochemical Test 2-Pack $29.99, accessed on 7/2/2016. https://www.pblabs.com/collections/fit-fecal-immunochemical-test/products/second-generation-fit-fecal-immunochemical-test-2-pack

4: Imperiale TF, Ransohoff DF, Itzkowitz SH, Turnbull BA, Ross ME; Colorectal Cancer Study Group. Fecal DNA versus fecal occult blood for colorectal-cancer screening in an average-risk population. N Engl J Med. 2004 Dec 23;351(26):2704-14. PubMed PMID: 15616205.

On 2016 Aug 24, Arturo Martí-Carvajal commented:

Dear authors,

I have read your valuable paper. However, at least for me, it is not clear how was conducted and reported statistical analysis in this crossover RCT. Why not reported SD and coefficient correlation? Why was only reported first phase as this RCT had been a parallel-design? Please, see table 2 of full text paper

I think that trial authors should report these statistical information.

Kind regards

Arturo Martí-Carvajal, MD Venezuela

On 2016 Jun 28, thomas samaras commented:

Certainly the authors have a point that hormonal and immunological characteristics affect the differences in longevity between men and women. However, women also have more complex bodies due to their reproductive role. In earlier years, females had similar or lower life expectancies compared to men. This was likely due to high death rates during birth from infections or birth complications without the benefits of modern medicine. Since many women in the past gave birth to many more children compared to today, they were obviously at high risk of reduced longevity.

There's another explanation for the difference in longevity between males and females. The larger size of males, who have the same same length telomeres at birth, exhibit faster shortening of telomeres with aging due to their bigger bodies and increased cell replication needs during their lifetimes. Maier et al. found shorter people at 90 years of age had longer telomeres and lived longer than taller people. Other studies have found shorter telomeres are related to increased CVD and reduced longevity (Cameron; Salpea). Studies of birds by Barrett some years ago and Ringsby (more recently) found that breeding for smaller size resulted in longer telomeres and reduced mortality.

Promislow and Moore in two different studies found that when male mammals are larger than females in a species, the males have greater mortality. And this increase in mortality correlates with increasing body mass. However, when females are larger within the same species, the females have a higher mortality. So body size differences appear to drive differences in mortality. Rollo observed this when he adjusted for differences in males and female body weight and found that the difference in longevity disappeared. Miller also found that when he compared human males and females of the same height, the difference in longevity was small. Poulain found that males and females in a mountainous village in Sardinia were equally likely of reaching centenarian status. Males averaged about 5'3 when they were young and no doubt somewhat taller than the women. However, the men spent the days in the fields or shepherding while the women stayed home. This paradox may be explained by a lower body weight for the men compared to the women.

Data from the Bulletin of WHO (1992) showed a consistent inverse relationship between male and female height differences and life expectancy. These findings are listed below. The first entry identifies the population, the second shows the percent increase in height for males compared to females and the third entry shows the decrease in life expectancy vs. increase in height.

1. 21 European countries averaged together: 7.3% vs. 7.5%

2. California White males vs. females: 9.0% vs. - 9.1%

3. California Asians males vs. females: 7.8% vs. - 7.7%

4. Califonria Hispanic males vs. females: 8.5% vs. - 9.3%

5. California Black males vs. females: 8.7% vs. - 11.7% (This difference may be due to much higher death rate due to violence among Black males)

6. US veterans (males vs. male): 6.4% vs. - 6.9%

7. Baseball players (male vs. male): 4.5% vs. - 4.4%

More recent data collected, included the US, Japan, and Poland. The results were essentially the same, including a comparison between Finnish basketball players vs. cross-country skiers (data provided by Sarna, et al.). The results were: basketball players were 8% taller and had an 8.7% shorter life expectancy.

On 2016 Jun 18, Christopher Southan commented:

This post provides a PubChem mapping for most of the compounds https://cdsouthan.blogspot.se/2016/06/antimalarial-structures-examined-for.html

On 2016 Jul 19, David Keller commented:

Is an opioid more toxic in extended-release than in immediate-release form, for the same total daily dose?

Ray and colleagues list a number of possible toxicities of opioids, and state that long-acting opioids (LAO's) "are of particular concern because the prolonged drug levels might increase toxicity." [1] This raises the question of whether chronic pain patients experience higher mortality due to the long-acting delivery system, and whether an equal daily dose of the same opioid would be safer if taken in divided doses of the immediate-release form. For example, a study comparing the mortality associated with extended-release oxycodone versus immediate-release oxycodone would answer the question of how much of the mortality associated with long-acting opioids in this study was due to the long-acting delivery of opioids versus the opioids themselves. Unfortunately, this study cannot answer that important question.

Ray et al cite a guideline that recommends long-acting opioids "for patients with frequent or constant pain", but which adds the provision: "Short-acting opioids may be used during the initial dose titration period of long-acting formulations and as rescue medication for episodes of breakthrough pain" [2] Another guideline states: "Short-acting opioids are probably safer for initial therapy [than LAO's] since they have a shorter half-life and may be associated with a lower risk of inadvertent overdose." [3] Both guidelines question the safety of initiating LAO's in opioid-naive pain patients and suggest that short-acting opioids (SAO's), taken only as-needed, might be inherently safer for initiating the treatment of chronic pain, at least until the patient has arrived at a stable opioid dosing regimen and developed some tolerance to its adverse effects.

eTable 6 in the Supplement to this study discloses that 96-97% of both the control group and the LAO group were currently taking any dose of SAO, but it is not possible to determine what percentage had been taking a stable total daily dose of SAO's long enough to have completed titration to efficacy and developed tolerance to harms such as respiratory depression. In other words, how much mortality was caused by premature treatment with LAO's of patients who had not taken SAO's long enough to complete dose titration and develop opioid tolerance?

References

1: Ray WA, Chung CP, Murray KT, Hall K, Stein CM. Prescription of Long-Acting Opioids and Mortality in Patients With Chronic Noncancer Pain. JAMA. 2016 Jun 14;315(22):2415-23. doi: 10.1001/jama.2016.7789. PubMed PMID: 27299617.

2: McCarberg BH, Barkin RL. Long-acting opioids for chronic pain: pharmacotherapeutic opportunities to enhance compliance, quality of life, and analgesia. Am J Ther. 2001 May-Jun;8(3):181-6. Review. PubMed PMID: 11344385.

3: Chou R, Fanciullo GJ, et al. American Pain Society-American Academy of Pain Medicine Opioids Guidelines Panel. Clinical guidelines for the use of chronic opioid therapy in chronic noncancer pain. J Pain. 2009 Feb;10(2):113-30. doi: 10.1016/j.jpain.2008.10.008. PubMed PMID: 19187889; PubMed Central PMCID: PMC4043401.

On 2016 Jun 17, David Keller commented:

"Long-Acting Opioids Increase Mortality in Patients With Chronic Noncancer Pain" - erroneous Practice Update headline

Through no fault of the investigators of this trial, the headline over the Practice Update summary of this study mistakes the association demonstrated in this observational study for causality, which can only be proved by means of a prospective, randomized, head-to-head interventional trial comparing long-acting opioids with other options for treating chronic non-cancer pain. Until such results are available, the headline should read:

Long-Acting Opioids Are Associated With Increased Mortality in Patients With Chronic Noncancer Pain

This distinction is important, and is a frequent cause of confusion in writers of headlines about clinical trials. Because serious therapeutic mistakes result from over-valuing observational data, it is important to correct these erroneous headlines. Here is the link to Practice Update, accessed on 6/17/2016, containing the erroneous headline:

http://www.practiceupdate.com/content/long-acting-opioids-increase-mortality-in-patients-with-chronic-noncancer-pain/40326/55/6/1#commentarea

The primary-care expert who discusses this study for Practice Update is Peter Lin MD,CCFP, who writes: "Long acting opioids increase death? This is an important question but one that we can’t ethically answer with a study. Imagine getting consent for this study? We are trying to see if these medications would kill you. So we could not ethically randomize patients to long acting opioids versus antiepileptic or antidepressant treatment and see who dies faster." This comment misses the most important question raised, but not answered, in this paper.

The authors list a number of possible toxicities of opioids, and state that long-acting opioids (LAO's) "are of particular concern because the prolonged drug levels might increase toxicity." This raises the question of whether chronic pain patients experience higher mortality due to the long-acting delivery system itself, and whether an equal daily dose of the same opioid would be safer if taken in divided doses of the immediate-release form. For example, a study comparing the mortality associated with extended-release oxycodone versus immediate-release oxycodone would answer the question of how much of the mortality associated with long-acting opioids in this study was due to the long-acting delivery of opioids versus the opioids themselves. Only by comparing an intrinsically short-acting opioid, such as oxycodone, with its extended-release form, in a head-to-head randomized study, can we isolate and quantify any increased harm of the extended-release delivery system itself. Such a trial would be ethical if the subjects were pain patients who are stable on a short-acting opioid and have been designated as appropriate candidates to switch to the extended-release form. The control group would delay that change for a month, while the intervention group would switch to extended-release immediately. Any difference in harms between these two groups during the first month could then be definitely attributed to the extended-release delivery system itself, because all other variables would be held constant, including the pain medication molecule.

Only a randomized, controlled, head-to-head trial, such as proposed above, can quantify the harms and benefits caused by the extended-release delivery of an opioid molecule as compared with the same total daily dose of the immediate-release form of the same opioid molecule. Answering this fundamental question is necessary before further comparisons can be interpreted, such as between opioid pain medications with differing intrinsic durations of effect, or comparisons between opioids and nonopioid pain treatments.

On 2016 Aug 16, Michelle Kraft commented:

Unfortunately I find this a very limited study. There are several point of care tools that should have been consulted in addition to UpToDate if the authors wanted a comprehensive understanding of the clinical impact of medical journals in point of care tools.<br> Additionally there are several other methods for studying reach and possible impact of journal articles such as altmetrics. A more robust article featuring several point of care products that included different types of altmetrics, while not perfect, would have given a much better picture of clinical impact of medical journals compared to the traditional impact factor.

On 2017 Apr 07, Janelia Neural Circuit Computation Journal Club commented:

Highlight/Summary Wilson and colleagues measured the orientation selectivity of dendritic spines on layer 2/3 pyramidal neurons in ferret visual cortex using two-photon calcium imaging. They are trying to address the question of how tuned output is produced by neurons that receive diverse types of input, a core question in neural computation. They suggest that higher orientation selectivity of individual neurons was correlated with greater clustering of similarly tuned spines (and not a narrower distribution spine preference or residence in a low-rate-of-change location of the orientation preference map). They conclude that dendritic nonlinearities play a critical role in shaping orientation selectivity.

Impact / strengths This is the first study of the functional organization of synaptic input onto the dendrites in a cortical region with columnar architecture. Previous work in mouse visual cortex (Jia et al., 2010) -- which lacks a columnar organization of orientation -- found no evidence of spatial clustering of input orientation preference on the dendrites of layer 2/3 neurons. On a technical level, this work is among only a handful of studies that have used genetically-encoded calcium indicators to estimate the functional selectivity of input to individual spines (cf Chen et al 2013).

By combining two-photon imaging of the dendritic arbor with intrinsic imaging of the orientation preference map, an impressive amount of information was gathered for each neuron. Although the number of neurons was modest (N=9), the number of identifiable spines imaged per neuron (N~300) is respectable for addressing questions of clustering. Signal-to-noise ratio at individual spines was also relatively high, comparable to previous studies (Chen et al., 2013).

Weaknesses The conclusions of this paper are critically dependent on the estimation of calcium influx through synaptic NMDA-Rs and contributions of local-dendritic calcium signals, as well as their interactions. Dendritic electrical events, including local synaptic potentials, local dendritic spikes, and depolarization produced by more global back-propagation of action potentials, cause dendritic calcium influx through voltage gated calcium channels (VGCCs) and also modulate NMDA-Rs. Depolarization interacts non-linearly with NMDA-R Ca influx. The field has not yet converged on methods to disambiguate global and local contributions to spine calcium signals. This is a critical issue for the key claim of the paper (‘clustering of similarly tuned spines’). For example, do the apparent clusters of similarly tuned spines drive the cell (the interpretation that is offered)? Or does the postsynaptic response at an optimal stimulus for the cell potentiate NMDA-R Ca influx in spines to produce an apparent cluster?

Wilson and colleagues estimate the spine signal by subtracting a linear fit of the spine fluorescence against the dendritic fluorescence. They then apply four inclusion criteria (pg 1004 and Methods). After this procedure, spines with orientation preference similar to the parent soma have similar tuning to spines with orthogonal orientation preference; this they take as an indication that the subtraction was effective. Given that some of the inclusion criteria are related to tuning curves (e.g., tuning must be well-described by a Gaussian fit) it was not clear if the inclusion criteria themselves biased this analysis. We would have welcomed analyses of the robustness of the results to changes in the parameters of the subtraction procedures and inclusion criteria.

A related concern is about the spatial scale of the dendritic hotspots. The size of the hotspots is not much smaller than the field-of-view of the images. The inclusion criteria (e.g., a Gaussian fit must explain 70% of the variance) have a possibly strong but unevaluated effect on the results.

On 2016 Sep 27, David Nunan commented:

Important methodological flaws limit the findings from the paper by Ravnskov and colleagues

We performed a post-publication critical appraisal of this paper and found a number of methodological flaws not least: 1. Lack of a published protocol 2. Searching of only one database 3. Nonuniform application of inclusion/exclusion criteria 4. A lack of critical appraisal of the methods used in the included studies 5. No indication of the quality or uncertainty of the included data 6. Issues with the accuracy of data extraction, and, 7. A lack of controlling for confounding due to the effect of lipid-lowering treatment and HDL-C levels presenting major bias and more likely underpinning the majority of the observed inverse associations.

Based on the above identified flaws in the paper by Ravnskov and colleagues we concluded: "Given that the authors failed to account for significant confounding as well as the methodological weaknesses of both the review and its included studies, the results of this review have limited validity and should be interpreted with caution. At this time it would not be responsible, or evidence-based, for policy decisions to be made based on the results of this study".

Our full appraisal can be found on our website here: http://www.cebm.net/cebm-response-lack-association-inverse-association-low-density-lipoprotein-cholesterol-mortality-elderly-systematic-review-post-publication-pee/

On 2016 Jun 16, David Keller commented:

In the elderly, statins reduce heart attacks, strokes and, probably, mortality

Ravnskov and colleagues conclude that their analysis of observational data requires "re-evaluation of guidelines recommending pharmacological reduction of LDL-C in the elderly as a component of cardiovascular disease prevention strategies." [1] I disagree, because the guidelines they challenge were based on large, randomized, placebo-controlled, double-blinded prospective interventional trials, higher-quality studies yielding more convincing data than the observational studies examined by Ravnskov. Statisticians warn us that observational data can only demonstrate associations, not causality, and should only be used for hypothesis generation, not for treatment decisions.[2]

A meta-analysis of eight high-quality controlled trials, including over 24,000 subjects with average age 73 years, was performed by Savarese and colleagues in 2013, which proved that elderly patients with CV risk factors but without established cardiovascular (CV) disease actually do benefit from statin therapy. [3] Statin therapy significantly reduced heart attacks by over 39%, and reduced strokes by over 23%, and non-significantly reduced all-cause mortality by 5.9%, and CV mortality by 9.3%. Mortality trends did not reach significance due, in part, to early termination of studies required by the significant reductions in MI and stroke, which are the #1 and #3 causes of death for the elderly. If these studies could have ethically been continued, the trends in CV and all-cause mortality could only have strengthened.

Elderly patients with CV risk factors do benefit from pharmacologic reduction of LDL-C by suffering fewer heart attacks, strokes and probably reduced mortality. Seniors should not discontinue statin therapy due to this study, which is based on lower quality data than the treatment guidelines are based on.

This comment has been published as an online letter by BMJ Open. [4]

References

1: Ravnskov U, et al. Lack of an association or an inverse association between low-density-lipoprotein cholesterol and mortality in the elderly: a systematic review. BMJ Open. 2016 Jun 12;6(6):e010401. doi:10.1136/bmjopen-2015-010401. PubMed PMID: 27292972.

2: Hannan EL. Randomized clinical trials and observational studies: guidelines for assessing respective strengths and limitations. JACC Cardiovasc Interv. 2008 Jun;1(3):211-7. doi:0.1016/j.jcin.2008.01.008. Review. PubMed PMID: 19463302.

3: Savarese G, et al. Benefits of statins in elderly subjects without established cardiovascular disease: a meta-analysis. J Am Coll Cardiol. 2013 Dec 3;62(22):2090-9.doi:10.1016/j.jacc.2013.07.069. Epub 2013 Aug 28. PubMed PMID: 23954343.

4: Keller DL, Statins do prevent heart attacks and strokes in the elderly. BMJ Open, published online on June 21, 2016 at the following URL: http://bmjopen.bmj.com/content/6/6/e010401.long/reply#bmjopen_el_9817

On 2016 Jun 15, David Keller commented:

The data in the included studies were all "corrected" under the assumption that LDL-C is a harmful risk factor

This analysis of multiple observational cohort studies reports no association, or an inverse association, between LDL-cholesterol levels and death rates, thereby challenging the widely-accepted hypothesis that high levels of LDL-C are a causal risk factor for cardiovascular atherosclerotic disease (CAD).

However, in table 2, we see that the study by Nilsson and colleagues was "corrected" for non-HDL-cholesterol, a variable which is highly correlated with LDL-C. The effect of correcting for non-HDL-C is almost the same as the effect of correcting for LDL-C itself, as we can see by using the Friedewald Equation to derive non-HDL cholesterol as LDL + Triglycerides/5 [1]

It appears that the authors of all of the analyzed cohort studies corrected their data under the assumption that higher LDL-C levels are harmful. Because Ravnskov is testing that very assumption, any "corrections" made to the original LDL-C data will actually further confound his findings. I suggest that Ravnskov reanalyze the original cohort data without any corrections or assumptions applied at all.

Reference

1: Martin SS, Blaha MJ et al, Friedewald-estimated versus directly measured low-density lipoprotein cholesterol and treatment implications. J Am Coll Cardiol. 2013 Aug 20;62(8):732-9. PubMed PMID: 23524048.

On 2016 Jun 22, Zvi Herzig commented:

The authors mistakenly exclude the possibility that increased gene suppression in e-cigarette users relates to nicotine:

Based on the similar serum cotinine levels in cigarette smokers and e-cigarette users, it does not appear that the overall difference in number and level of gene expression changes is dependent on nicotine.

However, unlike smoking, e-cigarette use frequently entails nasal exhalation (as online videos on the subject can demonstrate). It is already known that nicotine alone affects gene expression Zhang S, 2001, Bavarva JH, 2013. Nasal mucosae of e-cigarette users are exposed to much more nicotine, hence the increased gene suppression.

The health effects of nicotine exposure alone can be established from long-term human studies of snus and NRT use Murray RP, 1996, Lee PN, 2013, Royal College of Physicians, 2016.

On 2016 Jun 14, James Tsung commented:

Battlefield Acupuncture ASP Needle Insertion Video: https://youtu.be/xeEmX3jkvcE

Case 3 Pain from Carpel Tunnel Syndrome in 19 y.o. Female Video: https://youtu.be/oOujSLjcTFI

Case 4 Pain from Appendicitis in 9 y.o. Boy with Morphine Allergy Video: https://youtu.be/OlkJ2f1PP0I

A safer alternative to opioid analgesia by activating the placebo effect or more? More research to follow.

On 2016 Jul 28, Isabelle Boutron commented:

We would like to thank the Hilda Bastian for her interest in our work. We fully agree that our systematic review has some limitations and we acknowledged most of them in the paper. We also fully agree that the peer review system is a complex system and that we need different approaches to explore this system and that other study designs are also important to tackle this issue. We focused on randomised controlled trials as it provides a high level of evidence and one important result of this systematic review is the appalling lack of randomised controlled trials in this field. Despite huge human and financial investments in the peer review process, its essential role in biomedical research, only 7 RCTs have been published over the last 10 years. Yet, the conduct of randomised controlled trials in this field does not raise any important ethical or methodological concern. These results should be a call for action for editors to facilitate the conduct research in this field and give access to their data.

On 2016 Jun 12, Hilda Bastian commented:

This is a helpful broad brush update on randomized controlled trials (RCTs) of peer review interventions in biomedical journals (see older review Jefferson T, 2007 and my comment on that review). However, while the authors list several limitations, including restricting to RCTs and to biomedical journals, there are other limitations that, in turn, highlight the impact of those limitations.

One of those is the outcomes addressed here. The focus is explicitly on the peer reviews themselves and the process, and not wider outcomes, such as potential benefits and harms to peer reviewers or the impact of policies such as open review on journals (e.g. level of unwillingness to review).

In particular, the issue of harms brings us back to the limitation of looking only at RCTs, and limiting to the biomedical literature and a limited scope for databases searched. The authors provide no rationale for limiting the review to biomedical publications. Given that there are so few eligible studies within the scope this review, moving past this is essential. (In a blog post on anonymity, openness, and blinding of peer review in March 2015, in addition to the 11 RCTs identified in this systematic review, I identified a further 6 comparative studies, as well as other types of studies relevant to the questions around which known concerns exist.)

Peer reviewers are not just a means to an end: biases of peer reviewers can have a major impact on the careers of others, and at a minimum, specifically addressing gender, seniority, and institutional/country/language impact is critical to further work on this topic. A more contextual approach is needed to grapple with the complex ecosystem involved here.

A final point that is less likely to have had an impact, but is worth consideration by others working on this issue. Limiting the search strategy to the single term "peer review" may have an impact on searches, as terms such as open review and post-publication review become more widely used. Terms such as manuscript and editorial review, and peer reviewers could also be considered in constructing a search strategy in this area. (To identify the studies to which I refer above, Google Scholar and a wider range of search terms was necessary.)

(Disclosure: Part of my job includes working on PubMed Commons, which does not allow anonymous commenting.)

On 2016 Jun 27, Jafar Kolahi commented:

Editor’s note on this article is available via: http://www.nature.com/bdj/journal/v220/n11/full/sj.bdj.2016.398.html

On 2016 Jun 17, Jafar Kolahi commented:

Full list of Altmetric to 50 Dental Articles-2014 is available via:

http://www.nature.com/bdj/journal/v220/n11/extref/sj.bdj.2016.411-s1.pdf

On 2016 Jun 13, Christopher Tench commented:

The version of GingerALE employed had a bug that results in no control of the false positive results. This was fixed in version 2.3.6

On 2016 Aug 31, Clive Bates commented:

May I suggest that readers first read Professor Polosa's review below, and then turn to Benowitz NL, 2016 for a more credible and complete account of the cardiovascular effects of nicotine as they relate to e-cigarettes. Benowitz and Burbank review the relevant evidence and summarise the current state of knowledge as follows:

The cardiovascular safety of nicotine is an important question in the current debate on the benefits vs. risks of electronic cigarettes and related public health policy. Nicotine exerts pharmacologic effects that could contribute to acute cardiovascular events and accelerated atherogenesis experienced by cigarette smokers. Studies of nicotine medications and smokeless tobacco indicate that the risks of nicotine without tobacco combustion products (cigarette smoke) are low compared to cigarette smoking, but are still of concern in people with cardiovascular disease. Electronic cigarettes deliver nicotine without combustion of tobacco and appear to pose low-cardiovascular risk, at least with short-term use, in healthy users.

This should be a basis for reassuring and encouraging smokers considering switching to vaping.

As happens too often in this field, an author makes claims that go well beyond the scope of their scientific study or their field of expertise. Remarks made to media by the lead author at a cardiology conference in Rome caused a news storm in Britain, and will have increased interest in this paper. My examination of the basis for the claims made and reported is available on my blog > here.

On 2016 Aug 31, Riccardo Polosa commented:

The scientific letter lacks of many important details about participants' previous smoking history, type of device and e-liquid used in the study sessions.

Nonetheless, this is essentially an acute study showing what it is already know about the acute effect of nicotine on arterial stiffness. Besides, comparable acute changes in stiffness would also occur after drinking coffee (caffeine is not a risk factor for cardiovascular disease), exercising (exercise is beneficial for cardiovascular health), being exposed to emotional stress, and after taking nicotine replacement therapies.

Most of the observed changes in arterial stiffness after e-cigarette use were induced by asking participants to vape continuously for 30 min (!!!) (and only then the effect was similar to puffing a single conventional cigarette). Obviously, vaping continuously for 30 min is NOT a realistic conditions of use.

Besides, there are already two large clinical studies (one acute and the other chronic) that contradict the negative take of this research letter in relation to cardiovascular health:

http://www.ncbi.nlm.nih.gov/pubmed/24958250

http://www.ncbi.nlm.nih.gov/pubmed/26749533

Last but not least, measurement of arterial stiffness after acute exposure to active stimuli has no prognostic value whatsoever. That is why current guidelines on arterial stiffness measurements clearly state that before the measurements subjects should abstain from the use of any stimulants (like nicotine, caffeine and alcohol) for at least 4-6 hours.

On 2016 Jun 18, Zvi Herzig commented:

Drinking coffee also acutely increases aortic stiffness and blood pressure Vlachopoulos C, 2003. It is thus surprising that these transient effects are suggested as possible predictors of harm.