On 2016 Dec 29, Steve Alexander commented:

Oleamide (https://pubchem.ncbi.nlm.nih.gov/compound/5283387, called 9-octadecenamide here) has previously been investigated as a ligand at all three PPARs in vitro https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3414753/ Interesting to see the presence of other primary amides in the brain, notably palmitamide (https://pubchem.ncbi.nlm.nih.gov/compound/69421, called hexadecanamide here). An essential next couple of steps will be to identify the synthetic and degradative pathways associated with these ligands, and how/whether these compounds change with patho/physiological influences.

On 2016 Oct 24, Sean Ekins commented:

And here is post about why it took so long to reach Pubmed http://www.collabchem.com/2016/10/18/zika-homology-models-paper-makes-it-to-pubmed-6-months-after-publishing-in-f1000research/

On 2016 Oct 24, Sean Ekins commented:

more details and press release are here http://www.collabchem.com/2016/05/19/zika-open-becomes-openzika-on-ibm-world-community-grid/

On 2016 Oct 24, Sean Ekins commented:

Here is an update to the article in the form of slides - also goes into far more detail http://www.slideshare.net/ekinssean/open-zika-presentation

On 2016 Oct 18, Christopher Southan commented:

Ancilliary information https://cdsouthan.blogspot.se/2016/02/med-chem-starting-points-for-zika.html

On 2016 Nov 08, Jeffrey Gross commented:

Please be informed that the submission of our manuscript was cancelled within 24 hours of its initial submission to Experimental and Molecular Pathology. Unfortunately, and despite our many subsequent reminders, the journal went ahead and sent our paper for review and then published it online without our consent.

On 2017 Jan 12, Meg Waraczynski commented:

Thank you for your insights. In hindsight, we should have been much clearer in indicating that we were only strongly inferring the involvement of CaV1.3 channels in our behavioral results, but that we have no direct evidence for this. The inference was based on the facts reviewed in the Introduction, that (1) only CaV1 type channels have been linked to the activity of basal forebrain medium spiny neurons (reference 4); (2) of the CaV1 family, only 1.2 and 1.3 type channels are abundant in the brain (reference 3); and (3) the activation dynamics of 1.3 channels correspond much more closely to the activity state dynamics of medium spiny neurons than do the activation dynamics of 1.2 channels (reference 26). We hoped to use 1.3-specific drugs but, as noted in the Introduction, all such drugs we could find required the use of brain-toxic solvents. The dosages we used were selected based on dosages used by others who intracerebrally injected these drugs to affect behavior (references 1, 6, 7, and 16). We did not intend to focus on implicating CaV1.3 channels specifically in our observations, nor did we intend to have others use our paper as evidence that diltiazem and verapamil are CaV1.3-specific. We regret if this occurs. Our tentative conclusions as to the reward-relevant function of the system we are studying would remain the same even if it were found that our drug injections acted on mechanisms other than CaV1.3 channels specifically. We will be much more cautious when referring to this work in the future to emphasize these functional conclusions and not to implicate CaV1.3 channels specifically.

On 2017 Jan 03, Joerg Striessnig commented:

From a pharmacological point of view this is a very poor paper. It is common knowledge that verapamil and diltiazem have never been shown to be selective for Cav1.3 channels. Differential interaction with subdomains of the channel (their ref 19) has been studied with skeletal muscle channels and later with Cav1.2 (class C) L-type channels. Moreover, due to the higher concentrations for L-type channel block, verapamil and diltiazem also tend to inhibit other ion channels, such as Cav2 channels (PMIDs: 8574653, 10385261), at concentrations also inhibiting L-type channels. Here concentrations of 5 micrograms drug/0.5 microliter were infused, corresponding to about 20 mM concentrations, 10 times higher than the extracellular calcium concentration. There is no published evidence justifying their interpretation of a specific involvement of Cav1.3, as misleadigly mentioned even in the title. This interpretation by the authors and the failure by the reviewers to point out these limitations confuses readers and may even trigger further misleading experiments citing this paper as evidence for Cav1.3-selectivity of diltiazem and verapamil.

On 2016 Oct 26, Lydia Maniatis commented:

Natural scenes

The use of “natural scene statistics” is popular in current vision science and directly linked to its conceptual confusion.

In the words of the authors, “Biological systems evolve to exploit the statistical relationships in natural scenes….”

I want to first address the authors’ use of the term “natural scenes” and its implications, and move on to the problem of the validity and implications of the above quote in a subsequent comment.

“Natural scenes” is a very broad category, even broader given that the authors include in it man-made environments. In order to be valid on their own terms, the “statistics” involved – i.e. the correlations between “cues” and physical features of the environment – must hold across very different distances and orientations of the observer to the world, and across very different environments, including scenes involving close-ups of human faces.

Describing 96 photographs taken of various locations on the University of Texas campus from a height of six feet, a camera perpendicular to the ground, at distances of 2-200 meters as a theoretically meaningful, representative sample of “natural scenes” seems rather flakey. If we include human artifacts, then what count as “non-natural scenes” ?

The authors themselves are forced to confront (but choose to sidestep) the sampling problem when they note that “previous studies have reported that surfaces near 0° of slant are exceedingly rare in natural scenes (Yang & Purves, 2003), whereas we find significant probability mass near 0° of slant. That is, we find—consistent with intuition—that it is not uncommon to observe surfaces that have zero or near-zero slant in natural scenes (e.g., frontoparallel surfaces straight ahead).”

(Quite frankly, the authors’ intuition is causing them to confuse cause and effect, since we have a behavioral tendency to orient ourselves to objects so that we are in a fronto-parallel relationship to surfaces rather than in an oblique relationship to them, thus biasing the “statistics” in this respect).

They produce a speculative, technical and preliminary rationalization for the discrepancy between their distributions and those of Yang and Purves, leaving clarification to “future research.”

What they don’t consider is the sampling problem. Is there any doubt WHATSOEVER that different “natural scenes” - or different heights, or different angles of view, or different head orientations - will produce very different “prior probabilities”? If this is a problem, it isn’t a technical one.

On 2016 Oct 26, Lydia Maniatis commented:

Orientation isn’t prior to shape

The idea that slant/tilt are judged prior to shape, which Burge et al have adopted, suffers from the problems discussed above, and from empirical evidence that contradicts it.

The notion dates back at least to Marr’s 2.5D sketch. As Pizlo (2008) observes, “Marr assumed that figure-ground organization was not necessary for providing the percept of the 3D shape of an object” and asks “How could he get a way with this so long after the Gestalt psychologists had revolutionized perception by demonstrating the importance of figure-ground organization?”

Pizlo references experiments using wire objects (e.g. Rock & DiVita, 1987) that have shown that figure-ground organization is key to the shapes that actual 3D objects produce in perception, “even when binocular disparity or other depth cues are available.”

In general, if Marr had been correct in assuming that depth orientations of edges are prior to, and sufficient or necessary for, shape perception, then monocular perception would have no objective content, and 3D pictorial percepts would not occur, unless some special mechanisms had evolved just for this purpose.

In short, tilt-to-shape is not a principled, credible premise.

On 2016 Oct 26, Lydia Maniatis commented:

the right angle, and is linked to each of the other two, and each of the latter sit at the apex of acute angles, and are connected to each other. (What is being grouped are all the points inside of the perceptually constructed triangular outline).

If we now add a single point to the group, so that the set is compatible with a square, our rule will require that the connection between the two latter points be discarded, as both become the apex of right angles bounding a square and both are linked to the new point. This is, in fact, what happens in perception. So applying a rule to the three points, and a rule to the single point, locally, would not add up to the square contour, in principle; and does not, in perception.

Thus, when the authors assert that…

“the visual system starts with local measurements then combines those local measurements into the global representations; the more accurate the local measurements, the more accurate the global representation,”

…they are making an assertion that might sound simple and commonsensical to a layman (which is perhaps why it is so tenacious) but which is not justified for a vision scientist, any more than it is to say that we can build a house of cards one card at a time, or hear the sound of one hand clapping.

The use of “local cues” is a contemporary version of the reductionist approach to perception known as structuralism/introspectionism with its “sensory elements.” This approach couldn’t address the logical problem of organization of the visual field into shaped objects, discussed above, without invoking “experience” in a paradoxical and inconsistent fashion. “Cues” are similarly impotent.

On 2016 Oct 25, Lydia Maniatis commented:

As discussed, the best the authors could achieve in predicting measured “3D tilt” using their cues was not very good. Nevertheless, they describe their results as “complex,” “rich” and “detailed” in the sense that they feel able to discern some patterns in the generally inaccurate data that might be theoretically important or useful. For example, they say performance was often better when the three cues were in agreement. They propose to go on to compare performance of the model to performance of humans in psychophysical experiments. It seems to me that an important step to take prior to psychophysical testing is to test the model on its own terms; that is, to take a second set of “natural” images (perhaps of a different campus, or a national park) and test whether the ad hoc model derived from the first set will produce a qualitatively similar dataset. Will the two datasets, in all their richness and complexity, be mutually, statistically consistent? How will the authors compare them? If the data do not prove qualitatively repeatable, then p/p experiments would seem premature.

p.s. The open-endedness of the term "natural scene," in which the authors include man-made environments, imposes quite a serious replicability burden on the model. (The sampling problem (assuming the inductive approach was viable) includes the fact that arguably more time is spent by humans looking at human faces and bodies than at trees and shrubs). How many "scenes" should we test? Nevertheless, at least one attempt seems a minumum.

On 2016 Oct 22, Lydia Maniatis commented:

Part 1 This paper is all too similar to a large proportion of the vision literature, in which fussy computations thinly veil a hollow theoretical core, comprised of indefensible hypotheses asserted as fact (and thus implicitly requiring no justification), sometimes supported by citations that only weakly support them, if at all. The casual yet effective (from a publication point of view) fashion in which many authors assert popular (even if long debunked) fallacies and conjure up other pretexts for what are, in fact, mere measurements without actual or potential theoretical value is well on display here.

What is surprising in, perhaps, every case, is the willful empirical agnosia and lack of common sense, on every level – general purpose, method, data analysis - necessary to enable such studies to be conducted and published. A superficial computational complexity adds insult to injury, as many readers may wrongly feel they are not competent to understand and evaluate the validity of a study whose terms and procedures are so layered, opaque and jargony. However, the math is a distraction.

Unjustified and/or empirically false assumptions and procedures occur, as mentioned, at every level. I discuss some of the more serious ones below (this is the first of a series of comments on this paper).

1. Misleading, theoretically and practically untenable, definitions of “3D tilt” (and other variables).

The terms slant and tilt naturally refer to a geometrical characteristic of a physical plane or volume (relative to a reference plane). The first sentence of Burge et al’s abstract gives the impression that we are talking about tilt of surfaces: “Estimating 3D surface orientation (slant and tilt) is an important first step toward estimating 3D shape. Here, we examine how three local image cues …should be combined to estimate 3D tilt in natural scenes.” As it turns out, the authors perform a semantic but theoretically pregnant sleight of hand in the switch from the phrase “3D surface orientation (slant and tilt)” to the phrase “3D tilt” (which is also used in the title).

The obvious inference from the context is that the latter is a mere short-hand for the former. But it is not. In fact, as the authors’ finally reveal on p. 3 of their introduction, their procedure for estimating what they call “3D tilt” does not allow them to correlate their results to tilt of surfaces: “Our analysis does not distinguish between the tilt of surfaces belonging to individual objects and the tilt (i.e. orientation [which earlier was equated with “slant and tilt”]) of depth discontinuities…We therefore emphasize that our analysis is best thought of as 3D tilt rather than 3D surface tilt estimation.”

“3D tilt” is, in effect, a conceptually incoherent term made up to coincide with the (unrationalised) procedure used to arrive at certain measures given this label. I find the description of the procedure opaque, but as I am able to understand it, small patches of images are selected, and processed to produce “3D tilt” values based on range values collected by a range finder within that region of space. The readings within the region can be from one, two, three, four, or any number of different surfaces or objects; the method does not discriminate among these cases. In other words, these local “3D tilt values” have no necessary relationship to tilt of surfaces (let alone tilt of objects, which is more relevant (to be discussed) and which the authors don’t address even nominally). We are talking about a paradoxically abstract, disembodied definition of “3D tilt.” As a reader, being asked to “think” of the measurements as representing “3D tilt” rather than “3D surface tilt” doesn’t help me understand either how this term relates, in any useful or principled way, to the actual physical structure of the world, nor to the visual process that represents this world. The idea that measuring this kind of “tilt” could be useful to forming a representation of the physical environment, and that the visual system might have evolved a way to estimate these intrinsically random and incidental values, is an idea that seems invalid on its face - and the authors make no case for it.

They then proceed to measure 3 other home-cooked variables, in order to search for possible correlations between these and “3D tilt.” These variables are also chosen arbitrarily, i.e. in the absence of a theoretical rationale, based on: “simplicity, historical precedence, and plausibility given known processing in the early visual system.” (p. 2). Simplicity is not, by itself, a rationale – it has to have a rational basis. At first glance, at least the third of these reasons would seem to constitute a shadow of a theoretical rationale, but it is based on sparse, premature and over-interpreted physiological data primarily of V1 neuron activity. Furthermore, the authors’ definitions of their three putative cues: disparity gradient, luminance gradient, texture gradient, are very particular, assumption-laden, paradoxical, and unrationalised.

For example, the measure of “texture orientation” involves the assumption that textures are generally composed of “isotropic [i.e. circular] elements” (p. 8). This assumption is unwarranted to begin with. Given, furthermore, that the authors’ measures at no point involve parsing the “locations” measured into figures and grounds, it is difficult to understand what they can mean by the term “texture element.” Like tilt, reference to an “isotropic texture element” implies a bounded, discrete area of space with certain geometric characteristics and relationships. It makes no sense to apply it to an arbitrary set of pixel luminances.

Also, as in the case of “3D tilt” the definition of “texture gradient” is both arbitrary and superficially complex: “we define [the dominant orientation of the image texture] in the Fourier domain. First, we subtract the mean luminance and multiply by (window with) the Gaussian kernel above centered on (x, y). We then take the Fourier transform of the windowed image and comute the amplitude spectrum. Finally, we use singular value decomposition ….” One, two, three….but WHY did you make these choices? Simplicity, historical precedence, Hubel and Wiesel…?

If, serendipitously, the authors’ choices of things to measure and compare had led to high correlations, they might have been justified in sharing them. But as it turns out, not surprisingly, the correlations between “cues” and “tilt” are “typically not very accurate.” Certain (unpredicted) particularities of the data which to which the authors speculatively attribute theoretical value (incidentally undermining one of their major premises) will be discussed later.

On 2016 Oct 19, Jonathan Eisen commented:

Note - I am one of the authors of this paper.

There is a sentence in the paper that could be worded more carefully. I was pointed to this by a colleague. The sentence is "Gordonia sp. strain UCD-TK1 contains 5,032 coding sequences, and 64 noncoding RNAs."

It would be more accurate to say "The annotation of Gordonia sp. strain UCD-TK1 contains predicted 5,032 coding sequences, and 64 putative noncoding RNAs."

This would make it more clear that we do not have experimental evidence regarding how many coding sequences or ncRNAs are present in this organism.

On 2017 Jul 02, Karsten Suhre commented:

I think these PubMed pages should be a bit more self-explanatory - I came to this page while searching for "Metabolomic profiles delineate potential role for sarcosine in prostate cancer progression."

On first view this looked to me as if there was a research misconduct problem with this paper. However, after reading through the linked PMC document, I learned that the contrary was the case: The papers listed here have been plagiarized in an NIH grant application.

These papers are the victims, not the perpetrators - but on first glance this web site suggests otherwise.

On 2017 Jun 02, Eric Robinson commented:

The method and analysis adopted in this research are flawed and the conclusions are incorrect.

Action before commenting on pubmed: I contacted the journal and the authors in question with my concerns. The journal ignored a number of my emails and after an internal review decided not to issue a correction or retraction. I requested the results of the internal review, but the journal has not responded. The first author appears to have been a Masters student at the senior author’s institute and I was unable to contact the first author. The senior author (BM Corfe) informed me on the telephone that he was not prepared to discuss the research and instead advised me to raise any points in a public domain. The senior author also advised me that he would not be considering a correction or retraction of the work and that the research team stood by all of the conclusions made. Given the journal’s position on the study and my frustration with their handling of this, I was not prepared to support the journal by publishing a letter to the editor.

Research question: The researchers wanted to examine whether there is a link between self-reported appetite (self-reported subjective feelings of hunger) and energy intake; do participants who report feeling hungry eat more than participants who report feeling less hungry? They conducted what they described as a ‘systematic’ review and examined over 400 articles.

Conclusions drawn: The authors conclude that self-reported appetite (e.g. subjective feelings of hunger) ‘does not predict energy intake’ (title of article) and an associated University press release stated that ‘there is no link between how hungry we feel and the amount of calories we consume’.

Is this a spoof or hoax article? At first I thought this article may be a hoax, because the conclusion that self-reported hunger is in no way predictive of how much a person eats, is odd. Previous research shows that self-reported hunger/appetite does predict how much a person eats, but as you might expect, the correlation between self-reported hunger and energy intake is not perfect. Recently, Sadoul et al. (1) show this to be the case in an analysis of 23 studies that assessed self-reported appetite and ad-libitum meal energy intake. Robinson et al. (2) show this to the case in an analysis of 31 studies that assessed self-reported hunger and ad-libitum intake of snack foods.

Flawed method: There are a number of texts on best practice for conducting systematic reviews and synthesising data from multiple studies. Rather than using standard meta-analytic methods (e.g. combining weighted correlation coefficients between self-reported hunger and energy intake from studies), the researchers scored each study in their review as either providing evidence of a ‘link’ or evidence of ‘no link’ between self-reported hunger and energy intake. The scoring system used was inappropriate in a number of ways. For example, if an experimental manipulation in a study led to a change in energy intake without a change in self-reported hunger, in the present review this constituted evidence that self-reported hunger does not predict energy intake. This line of reasoning is a logical fallacy because it is based on the premise that a) energy intake can only be affected by self-reported hunger and b) energy intake being affected by anything other than subjective feelings of hunger proves that subjective appetite is in no way related to energy intake. Energy intake can be increased or decreased by a multitude of factors and many of these will not act on energy intake by altering self-reported hunger.

Flawed analysis: The authors’ main analysis was dependent on counting studies that provided statistically significant findings vs. those that did not, which is not considered best practice as it ignores considerations of sample size, statistical power and how heavily each study should be weighted in analyses. The above points aside, the authors went on to report that approximately 49% of studies they surveyed found a ‘link’ and 51% found ‘no link’ between subjective self-reported hunger and energy intake. This is actually highly convincing evidence that there is a link between self-reported hunger and energy intake, because if there was ‘no link’ we would expect to see closer to only 5% of all studies finding a ‘link’ (typical alpha level of .05), as opposed to the 49% reported.

Invalid conclusions: A combination of flawed methods and analyses results in incorrect conclusions.

A sobering experience: I noticed this study because of the bizarre conclusion it made; hunger in no way relates to how much we eat. I reached out to the authors several times over email. In the end I had to ring the senior author’s office phone to speak to him, but as noted the senior author was not prepared to discuss his research or revise his position on this research. This to me is direct experiential evidence that some scientists do not appear to care about the quality and accuracy of research they conduct and publish.

(1) Sadoul BC, Schuring EA, Mela DJ, Peters HP. The relationship between appetite scores and subsequent energy intake: an analysis based on 23 randomized controlled studies. Appetite 2014; 83: 153-159

(2) Robinson E, Haynes A, Hardman CA, Kemps E, Higgs S, Jones A. The bogus taste test: Validity as a measure of laboratory food intake. Appetite 2017; 116: 223-231.

On 2017 Mar 20, Prajak Barde commented:

One of the objective of the meta-analysis by Bai B et al is to assess the relationship between human cytomegalovirus and colorectal cancer (CRC) risk. Author analyzed four studies to demonstrate that tumor tissues had a significantly higher rate of HCMV infection (OR = 6.59, 95% CI = 4.48–9.69), thus confirming that CRC tissue is significantly burdened with HCMV DNA as compared to adjacent normal tissues. However, it is not clear how the conclusion of an increased risk of CRC due to HCMV infection is drawn. As detection of HCMV DNA in CRC tissues by itself don’t provide adequate evidence to prove the causal role of HCMV in CRC, further explanation is needed to justify increased risk of CRC due to HCMV infection. In addition, in light of multiple etiological factors responsible for causation of CRC (e.g. insufficient activity, high-fat diets, smoking and living in a developed country)2, the increased risk associated with HCMV in relation to these risk factors also need to be ascertained and established.

There are diagnostic challenges in detecting HCMV, due to “hit and run” mechanism of virus, though author considered PCR technique that showed higher positive rate than In situ hybridization (ISH) and immunohistochemistry (IHC),3 the validity of “negative results” of studies considered for meta-analysis should be ascertained before drawing any conclusion based on these results.

On 2016 Nov 18, Daniel Corcos commented:

Welch et al. assume wrongly that breast cancer incidence has been stable after the advent of screening mammography, although they find 132 more cases of BC a year per 100,000 women in the period following screening implementation. To justify this strange assumption they argue: “Those who postulate such substantial increases in underlying incidence, however, must explain why the increase coincides temporally with the introduction of screening, and why the incidence of the most aggressive form of the disease — metastatic breast cancer — remains essentially unchanged”. It is perfectly possible to explain both observations by the fact that early treatment is protective against metastasis, as expected and known for a century, and by the fact that mammography screening induces breast cancer at a much higher rate and with a shorter delay than usually expected.

References

Bleicher RJ, Ruth K, Sigurdson ER, et al. Time to Surgery and Breast Cancer Survival in the United States. JAMA Oncol 2016;2:330-9. Mathews FS. The Ten-Year Survivors of Radical Mastectomy. Ann Surg 1933;98:635-43.

On 2017 Mar 20, Miguel Lopez-Lazaro commented:

Pancreatic cancer formation is gradual

It is widely accepted that cancer development requires the sequential accumulation of DNA changes over years or decades. In this article, Notta et al. challenge this dogma. They analysed the genomes of more than 100 pancreatic tumours and found that many DNA changes occur simultaneously as a consequence of massive genomic rearrangements associated with catastrophic mitotic events. The authors discuss that the formation of advanced pancreatic cancers is not gradual, and propose a new model in which the simultaneous accumulation of genetic alterations arising from mitotic errors rapidly leads to the development of invasive disease. However, cancer incidence data by age indicate that the time frame required for the formation of invasive pancreatic cancers is similar from other cancers in which these mitotic errors are rare, thereby indicating that the high frequency of catastrophic mitotic events in pancreatic tumours may be a consequence of the disease rather than a cause. In addition, the extremely low rates of pancreatic cancer in young people and the striking increase in its incidence with age strongly suggests that the formation of most invasive pancreatic cancers requires the gradual accumulation of DNA changes over several decades. This means that there is time and opportunity to detect and stop pancreatic carcinogenesis before the development of advanced disease.

Full text at http://dx.doi.org/10.13140/RG.2.2.16865.92009

On 2017 Sep 28, William Davies commented:

Further evidence for a link between STS activity and Ctgf/Ccn2 expression has recently been obtained from in vivo and in vitro models of colorectal cancer (Gilligan et al., Estrogen Activation by Steroid Sulfatase increases Colorectal Cancer proliferation via GPER J Clin Endocrinol Metab. 2017 doi: 10.1210/jc.2016-3716)

On 2017 Aug 08, Christopher Tench commented:

Could you possibly provide the coordinates analysed otherwise it is difficult to interpret the results.

On 2017 Jul 02, Suzy Chapman commented:

ICD-11 Beta draft: Rationale for Proposal for Deletion of proposed new category: Bodily distress disorder

March 8, 2017

Full text:

http://wp.me/pKrrB-4dc

References:

1 Creed F, Guthrie E, Fink P, Henningsen P, Rief W, Sharpe M, White P. Is there a better term than “medically unexplained symptoms”? J Psychosom Res. 2010 Jan;68(1):5-8. doi:10.1016/j.jpsychores.2009.09.004. [PMID: 20004295]

2 Fink P, Schröder A. One single diagnosis, bodily distress syndrome, succeeded to capture 10 diagnostic categories of functional somatic syndromes and somatoform disorders. J Psychosom Res. 2010 May;68(5):415-26. [PMID: 20403500]

3 Creed F, Gureje O. Emerging themes in the revision of the classification of somatoform disorders. Int Rev Psychiatry. 2012 Dec;24(6):556-67. doi: 10.3109/09540261.2012.741063. [PMID: 23244611]

4 Gureje O, Reed GM. Bodily distress disorder in ICD-11: problems and prospects. World Psychiatry. 2016 Oct;15(3):291-292. doi: 10.1002/wps.20353. [PMID: 27717252]

5 American Psychiatric Association. (2013). Somatic Symptom and Related Disorders. In Diagnostic and statistical manual of mental disorders (5th ed.). Washington, DC: Author.

6 Frances A, Chapman S. DSM-5 somatic symptom disorder mislabels medical illness as mental disorder. Aust N Z J Psychiatry. 2013 May;47(5):483-4. [PMID: 23653063]

7 Lam TP, Goldberg DP, Dowell AC, Fortes S, Mbatia JK, Minhas FA, Klinkman MS. Proposed new diagnoses of anxious depression and bodily stress syndrome in ICD-11-PHC: an international focus group study. Fam Pract. 2013 Feb;30(1):76-87. doi: 10.1093/fampra/cms037. Epub 2012 Jul 28. [PMID: 22843638]

8 Ivbijaro G, Goldberg D. Bodily distress syndrome (BDS): the evolution from medically unexplained symptoms (MUS). Ment Health Fam Med. 2013 Jun;10(2):63-4. [PMID: 24427171]

9 Goldberg DP, Reed GM, Robles R, Bobes J, Iglesias C, Fortes S, de Jesus Mari J, Lam TP, Minhas F, Razzaque B et al. Multiple somatic symptoms in primary care: A field study for ICD-11 PHC, WHO’s revised classification of mental disorders in primary care settings. J Psychosom Res. 2016 Dec;91:48-54. doi:10.1016/j.jpsychores.2016.10.002. Epub 2016 Oct 4. [PMID: 27894462]

10 Medically Unexplained Symptoms, Somatisation and Bodily Distress: Developing Better Clinical Services, Francis Creed, Peter Henningsen, Per Fink (Eds), Cambridge University Press, 2011.

11 Frances Creed and Per Fink. Presentations, Research Clinic for Functional Disorders Symposium, Aarhus University Hospital, May 15, 2014.

12 Rief W, Isaac M. The future of somatoform disorders: somatic symptom disorder, bodily distress disorder or functional syndromes? Curr Opin Psychiatry September 2014 – Volume 27 – Issue 5 – p315–319. [PMID: 25023885]

13 Chalder, T. An introduction to “medically unexplained” persistent physical symptoms. Presentation, Department of Psychological Medicine, King’s Health Partners, 2014. [Accessed 27 February 2017]

14 Schumacher S, Rief W, Klaus K, Brähler E, Mewes R. Medium- and long-term prognostic validity of competing classification proposals for the former somatoform disorders. Psychol Med. 2017 Feb 9:1-14. doi: 10.1017/S0033291717000149. [PMID: 28179046]

15 Fink P, Toft T, Hansen MS, Ornbol E, Olesen F. Symptoms and syndromes of bodily distress: an exploratory study of 978 internal medical, neurological, and primary care patients. Psychosom Med. 2007 Jan;69(1):30-9. [PMID: 17244846]

16 Carroll L. Alice’s Adventures in Wonderland. 1885. Macmillan.

On 2016 Dec 17, Suzy Chapman commented:

Firstly, it is to be welcomed that authors Gureje and Reed have published this progress report on the work of the ICD-11 Somatic Distress and Dissociative Disorders Working Group (S3DWG) in an open access journal. The revision of ICD cannot be described as a "transparent and inclusive" process when ICD revision Topic Advisory Groups and sub working groups publish progress reports and rationales for their proposals behind paywalls.

I note the paper discusses the S3DWG's rationale for not including the word "somatic" in the name it proposes for its prototype disorder.

There is, however, no discussion within the paper of the sub working group's rationale for proposing to use the disorder term "Bodily distress disorder (BDD)" when this term is already being used interchangeably in the literature [1-4] with "Bodily distress syndrome (BDS)" - a divergent construct and criteria set already operationalized in Denmark, in clinical and research settings [5].

Omission of consideration within this paper of the potential impact for maintaining construct integrity within and beyond ICD-11 is troubling.

The S3DWG's "Bodily distress disorder" construct, as defined for the ICD-11 core version, has strong conceptual congruency and characterization alignment with DSM-5's "Somatic symptom disorder (SSD)" and poor conceptual and characterization alignment with Fink et al (2010) "Bodily distress syndrome."

It is noted that "Somatic symptom disorder" is also inserted into the ICD-11 Beta draft under Synonyms for BDD.

In sum:

ICD-11's proposed BDD is more closely aligned with DSM-5's SSD (Gureje and Reed, 2016).

The term "BDD" is already used interchangeably in the field for the operationalized "BDS" disorder construct [1-4].

That DSM-5's SSD and Fink et al's (2010) BDS are "very different" concepts, with different criteria sets, capturing different patient populations has been acknowledged by SSD work group chair, Joel E Dimsdale, and by Per Fink, Peter Henningsen and Francis Creed [6][7].

The unsoundness of introducing into ICD a new disorder category that proposes to use terminology that is already closely associated with a different (and already operationalized) construct/criteria set and the potential for conflation between the two has yet to be acknowledged or addressed by the sub working group responsible for this recommendation.

The S3DWG's choice of nomenclature needs referral back to the ICD-11 Revision Steering Group (RSG) and Joint Task Force (JTF) for urgent consideration of the implications of this proposed name for disorder integrity.

References:

1 An introduction to "medically unexplained" persistent physical symptoms, Presentation, Professor Trudie Chalder, Department of Psychological Medicine, King’s Health Partners, 2014, Slide #3 http://www.kcl.ac.uk/ioppn/depts/pm/research/imparts/Quick-links/Seminar-Slides/Seminar-7/Trudie-Chalder-intro.pdf

2 Rief W, Isaac M. The future of somatoform disorders: somatic symptom disorder, bodily distress disorder or functional syndromes? Curr Opin Psychiatry September 2014 - Volume 27 - Issue 5 - p 315–319 Rief W, 2014

3 Ivbijaro G, Goldberg D. Bodily distress syndrome (BDS): the evolution from medically unexplained symptoms (MUS). Ment Health Fam Med. 2013 Jun;10(2):63-4. Ivbijaro G, 2013

4 Fink P, Toft T, Hansen MS, Ornbol E, Olesen F. Symptoms and syndromes of bodily distress: an exploratory study of 978 internal medical, neurological, and primary care patients. Psychosom Med. 2007 Jan;69(1):30-9. Fink P, 2007

5 Fink P, Schröder A. One single diagnosis, bodily distress syndrome, succeeded to capture 10 diagnostic categories of functional somatic syndromes and somatoform disorders. J Psychosom Res. 2010 May;68(5):415-26. Fink P, 2010

6 Medically Unexplained Symptoms, Somatisation and Bodily Distress: Developing Better Clinical Services, Francis Creed, Peter Henningsen, Per Fink (Eds), Cambridge University Press, 2011

7 Francis Creed and Per Fink. Presentations, Research Clinic for Functional Disorders Symposium, Aarhus University Hospital, May 15, 2014.

On 2016 Dec 20, David Keller commented:

Effects of Rheumatoid Arthritis, and Its Treatments, on Parkinson Disease

Sung and colleagues derived two new and independent hypotheses from this study. First, they observed an inverse association between rheumatoid arthritis (RA) and the risk of subsequent development of Parkinson disease (PD), consistent with the hypothesis that RA is protective against PD. Second, they observed that the risk of developing PD was reduced even more in RA patients treated with biological disease-modifying anti-rheumatic drugs (DMARDs) but not in patients treated without DMARDs or with non-biological DMARDs. [1] This led to their second hypothesis, that "biologic DMARDs appear to further reduce the PD risk" in RA patients (more so than treatment with non-biological DMARDs, or no DMARDs), suggesting a possible "role of biologic DMARDs in PD treatment".

In summary, the authors of this study propose two new hypotheses to fully explain their results:

Hypothesis #1: Rheumatoid Arthritis disease is protective against the onset of Parkinson disease.

Hypothesis #2: Biological DMARDS, as treatment for RA, confer additional protection against the onset of PD.

Sung and colleagues point out that Hypothesis #1 contradicts "the hypothesis that chronic inflammation in RA may increase the risk of developing PD", citing a recent study that, similarly, "identified an inverse association between PD and systemic lupus erythematosus", and another confirmatory study that "reported a 30% reduction in the risk of developing PD in patients with RA and systemic involvement" [Sung's references #23 and #24]. Sung mentioned that RA patients are more likely to take NSAIDs, and that certain NSAIDs have been found to be protective against PD, but Sung claims that the association of RA with protection from PD withstood controlling for NSAID use. In a separate comment, I will address the errors I believe Sung and colleagues made when correcting their data for NSAID use, and how those errors could falsely support Hypothesis #1, above.

However, suppose hypothesis #1 is true. The association of additional reduction of PD incidence with the use of biological DMARDs might not be due to their having an intrinsic neuroprotective effect, but, rather, to the fact that they are reserved for use in the most severe or refractory cases of RA. The increased level of RA disease activity and severity associated with the use of biological DMARDs could be the cause for the additional decreased risk of PD. The inability to distinguish whether the additional protection from PD was due to neuroprotective benefits of biological DMARDs, or due to the more severe RA which caused biological DMARDs to be "indicated" (medically needed), is an example of confounding by "indication bias".

Biological DMARDs have likely been compared with non-biological DMARDs in randomized clinical trials for treatment of rheumatoid arthritis. If these trials included data on the new onset of PD, they could be pooled in a meta-analysis to test Sung's Hypothesis #2.

Reference

Sung YF, Liu FC, Lin CC, et al. Reduced risk of Parkinson disease in patients with rheumatoid arthritis: A nationwide population-based study. Mayo Clin Proc. 2016;91(10):1346-1353.

On 2016 Dec 19, David Keller commented:

Only ibuprofen is associated with reduced PD risk - controlling for use of any NSAID introduces error

The following quote is from the above paper by Sung [1]:

"Previous studies [2,3] have reported that nonaspirin NSAIDs, particularly ibuprofen, may be associated with a reduced risk of developing Parkinson disease. However, after controlling for all comorbidities and NSAID use, patients with RA still exhibited a reduced risk of PD compared with patients without RA..." However, the two cited studies actually demonstrated that ibuprofen use is associated with significantly reduced risk of PD, but other commonly-used NSAIDs are not.

In a landmark paper published in 2011, but not cited by Sung, Gao and colleagues published a new observational trial, plus a comprehensive meta-analysis, which concluded that ibuprofen, but not other NSAIDs, is associated with a significant 38% reduction in risk for PD [4]. Therefore, the bolded phrase should be corrected to read: "ibuprofen, but not other NSAIDs, is associated with a significantly reduced risk of developing PD".

Sung and colleagues controlled for NSAID use, but not separately for ibuprofen use; their Table 3 presents 11 baseline variables, and the adjusted HR of each. NSAIDs are discussed together as a single group, exhibiting a small but significant 9% protective effect against PD, the result of diluting the larger 38% protection associated with ibuprofen with the lack of significant protection associated with other NSAIDs.

Thus, the HR of 0.91 used by Sung to control for the use of any NSAID systematically under-corrects for the protection from PD for patients who took ibuprofen, while systematically over-correcting when the NSAID used was not ibuprofen. To eliminate these systematic errors, the study data should be reanalyzed, and corrected specifically for ibuprofen use, rather than for the use of any NSAID.

Until this correction is made, it is unclear how much of the apparent protection associated with RA disease or with biological DMARDs was actually attributable to the use of ibuprofen.

In an unpublished reply to these arguments, Sung's group wrote: "[Keller's] criticism focuses on the issue whether [any] non-aspirin NSAID or ibuprofen only, has the truly protective effect against the development of PD". Sung and colleagues agreed that "ibuprofen was associated with decreased risk of PD, but not aspirin or other NSAIDs" and concluded that "ibuprofen use should be considered as an important covariable in future correlational research in PD." [5]

References

1: Sung YF, Liu FC, Lin CC, Lee JT, Yang FC, Chou YC, Lin CL, Kao CH, Lo HY, Yang TY. Reduced Risk of Parkinson Disease in Patients With Rheumatoid Arthritis: A Nationwide Population-Based Study. Mayo Clin Proc. 2016 Oct;91(10):1346-1353. doi: 10.1016/j.mayocp.2016.06.023. PubMed PMID:27712633.

2: Chen, H., Jacobs, E., Schwarzschild, M.A. et al, Nonsteroidal antiinflammatory drug use and the risk for Parkinson's disease. Ann Neurol. 2005;58:963–967.

3: Rees, K., Stowe, R., Patel, S. et al, Non-steroidal anti-inflammatory drugs as disease-modifying agents for Parkinson's disease: evidence from observational studies. Cochrane Database Syst Rev. 2011;:CD008454.

4: Gao X, Chen H, Schwarzschild MA, Ascherio A. Use of ibuprofen and risk of Parkinson disease. Neurology. 2011 Mar 8;76(10):863-9. doi:10.1212/WNL.0b013e31820f2d79. PubMed PMID: 21368281; PubMed Central PMCID: PMC3059148.

5: Sung YF, Lin CL, Kao CH, and Yang TY. Reply to Keller's unpublished letter to Mayo Clinic Proceedings. Received by email on November 22, 2016.

On 2018 Feb 02, Christopher Korch commented:

In this article by Binder et al. in PLOS ONE (Binder NK, 2016), the authors describe using the cell line ECC-1 as a model of endometrial tissue to study embryo implantation. Using recombinant human placental growth factor they found that treatment of ECC-1 cells increased their cellular adhesion to fibronectin-coated tissue culture plates. I wish to point out two major concerns about the authenticity of this cell line.

First, two of the three references which they cite for having characterized ECC-1 are not correct. References 23 and 24 refer to the cell line HES, which my colleagues and I showed in 2012, was actually the HeLa subline WISH; i.e., a cervical adenocarcinoma cell line (Korch et al. Korch C, 2012) and our finding was confirmed in 2014 by the originator of HES (Kniss & Summerfield Kniss DA, 2014). WISH was shown by SM Gartler in 1966-1970 to be HeLa cells (Gartler SM, 1967, Gartler SM, 1968, Auersperg N, 1970) and this has been confirmed numerous times thereafter (e.g., by Nelson-Rees during the 1970s-1980s Nelson-Rees WA, 1980, Nelson-Rees WA, 1981; Lavappa at the ATCC in 1978 Lavappa KS, 1978; and Masters et al. 2001, Sandler AN, 1992). No authentic sample of WISH is known to exist (see cell register of misidentified cell lines at the websites of the International Cell Line Authentication Committee (http://ICLAC.org) and of the Expasy Cellosaurus (https://web.expasy.org/cellosaurus/). In fact, ECC-1 is also listed on both websites as a misidentified cell line.

Next, the authors do not indicate whether they genetically authenticated their sample of ECC-1 (currently the method of reference is by STR genotyping). This cell line was developed by PG Satyaswaroop's group at the Hershey Medical Center in about 1985-1987 when it was established from a xenograft sample of the endometrial tumor EnCa101, which was being maintained by passaging in mice. The cell line ECC-1 was deposited at the ATCC by Bruce Lessey, who had received it from Dr. Sayaswaroop. It was STR genotyped by the ATCC. As described earlier by me and my colleagues (Korch C, 2012) from STR genotyping of numerous samples of ECC-1 and Ishikawa cells from various sources and comparison to the STR profile of the ATCC sample of this cell line, ECC-1 was found to be one of three cell lines - a derivative of the endometrial cell line Ishikawa developed by Nishida (see Nishida M, 2002 for history and dissemination of various subclones), the breast cancer cell line MCF-7, or a mixture of Ishikawa and MCF-7 cells. A complicating fact is that ISHIKAWA / ECC-1 is an MSI unstable cell line, giving rise to variable STR genotypes.

In an attempt to determine the expected STR profile of ECC-1 / EnCa101, the Hershey Medical Center was approached, but no samples of the original tumor (paraffin block, etc) could be found as the Satyaswaroop lab had been closed in 2002. Furthermore, none of the ECC-1 or Ishikawa samples matched any of the four samples of xenografts of the tumor EnCa101. This tumor has been maintained by VC Jordan since about 1987 (Gottardis MM, 1988). The earliest tumor sample that I could obtain of EnCa101was from 1987 and was found to be genetically unrelated to the three tumor xenograft samples of EnCa101 from 2009 (unpublished data) and the STR genotypes of these four samples did match the profile of any known cell line in several databases.

Therefore, these results using the cell line ECC-1 should be re-interpreted and used cautiously, because (1) this cell line is a misidentified cell line as shown earlier (Korch C, 2012) and is listed as a misidentified cell line on the ICLAC and Cellosaurus websites; (2) the true identity of the sample of ECC-1 that was used by the authors was not determined, (3) its provenance is confusing because two of the three references for its characterization are incorrect and refer to a different cell line, and (4) since the genetic identity of ECC-1 cell line was not checked, it could be one of at least five different cultures (three variants of Ishikawa and breast cancer cell line and a mixture of Ishikawa and MCF-7).

Hopefully, this will encourage others to authenticate their cell lines. Below are some suggestions of how this problem could be avoided in the future. They are based on ideas put forth earlier by Dr. Amanda Capes-Davis in a PubMed Commons Comment on another article of concern (see Xu HT, 2016).

Authors & Reviewers could use the aforementioned resources since: • STR genotyping is effective for authentication of human cell lines and is the consensus method for comparison of human cell line samples (American Type Culture Collection Standards Development Organization Workgroup ASN-0002., 2010, American Type Culture Collection Standards Development Organization Workgroup ASN-0002., 2010); and

• Checklists for the identity of cell lines used in manuscripts and grant applications are readily available at http://iclac.org/resources/cell-line-checklist/ and through Expasy Cellosaurus https://web.expasy.org/cellosaurus/.

Journals, their Editors, and Funding Organizations could: • Implement more stringent criteria for publication and funding of research because encouragement of authentication testing, although a step forward, is insufficient to stop use of misidentified cell lines.

• Develop an authentication policy for sake of reproducible research. For example, to meet this need the NIH has recently implemented requirements for authentication of key resources as part of grant applications (e.g. see NOT-OD-16-011, NOT-OD-16-012).

• Require testing using an accepted method of cell line authentication, which is effective as illustrated by the cell line authentication policy of the International Journal of Cancer (Fusenig NE, 2017). If the authors, the reviewers, or the journal editors had followed PLOS ONE's own guidelines (http://journals.plos.org/plosone/s/submission-guidelines#loc-cell-lines) and checked for the identity of this cell line on either the ICLAC website (http://iclac.org/databases/cross-contaminations/) or on the Cellosaurus website (https://web.expasy.org/cellosaurus/), the journal would have detected and avoided this problem prior to publication.

• Regularly review the efficacy of their policy on cell authentication testing to see whether it is adequate (as was done by the International Journal of Cancer), especially in light of such examples having been published by a journal that requires authentication of cell lines prior to submission of manuscripts.

On 2016 Nov 15, IRWIN FEINBERG commented:

Kurth et al base their study on a faulty premise, stated in the first sentence: “Brain networks respond to sleep deprivation or restriction (emphasis added) with increased sleep depth which is quantified as slow-wave activity (SWA) in the sleep electroencephalogram (EEG)…” In fact, there is now abundant evidence that sleep restriction does not increase SWA in subsequent sleep, although it produces strong increases in behavioral sleepiness. We first observed this result in a 1991 study of the effects of acute termination of the last 3.5 h of sleep. This decrease in sleep duration did not produce the expected increase in either visually scored or computer measured SWA Feinberg I, 1991. This result so surprised us that we immediately repeated the experiment in a new group of subjects and obtained the same result Travis F, 1991. Since it was well established that a night of total sleep deprivation increases SWA, we sought to determine how much sleep restriction is needed to increase SWA. We limited sleep to 100 min and found that this restriction increased SWA. However, the increased SWA after 100 min of sleep differed from that after a night of total sleep deprivation (TSD). Whereas TSD reduced both the amplitude and incidence of slow waves, restriction to 100 min of sleep increased SW incidence but not amplitude Feinberg I, 1988. Subsequently, an extensive study by van Dongen et al showed that sleep restriction to 4 h/night for 14 consecutive nights does not increase SWA although it produces intense sleepiness and impaired vigilance Van Dongen HP, 2003. The previous studies were done with young adults so that it remained possible that the young subjects Kurth et al studied might have a different SWA response to sleep restriction. This is not the case. Sleep restriction in late childhood also failed to increase SWA Campbell IG, 2016. An incidental but reliable observation in our previous studies was that TSD Feinberg I, 1979 and partial sleep deprivation by restricted sleep (studies cited above) both reduce eye movement density in REM sleep. None of this previous work is cited or discussed by Kurth et al. The omissions are especially regrettable for two reasons. First, the failure of sleep restriction to increase SWA illustrates one of the major predictive failures of recovery models of SWA (both our own Feinberg I, 1974 and the similar two-process model Borbély AA, 2016). Second, the suppressive effects of sleep loss on eye movement density holds major biological implications for interrelations among sleep depth, NREM and REM sleep. Kurth et al's disregard of previous, highly relevant, well-substantiated data impedes research progress.

On 2017 Mar 26, Harri Hemila commented:

Antioxidants are not equal: an example of the apples and oranges problem

In their network meta-analysis on treatments for contrast medium–induced acute kidney injury (CIAKI), Su X, 2017 pooled different vitamins to a single group of “vitamins and analogues” but in doing so ignored the fact that vitamin C is water soluble, whereas vitamin E is fat soluble, and therefore their effects might be quite different. This is an example of the apples and oranges problem. With an analogous reasoning, studies on ciprofloxacin and penicillin might be pooled together on the basis that they are ”antibiotics”, though they have quite different mechanisms and indications.

Su X, 2017 calculated an odds ratio (OR) = 0.64 for the effect of “vitamins and analogues” but they did not calculate the specific effects of vitamins E and C. From 9 vitamin C trials, Sadat U, 2013 concluded that vitamin C may prevent CIAKI and calculated a risk ratio (RR) = 0.67. From 3 vitamin E trials, Rezaei Y, 2017 calculated that vitamin E decreased the incidence of CIAKI with RR = 0.38 (95%CI 0.24-0.62). On the OR scale, the effect of vitamin E corresponds to OR = 0.34 (95%CI 0.20-0.58).

Thus, vitamin E seems to have a greater effect against CIAKI compared with vitamin C. These two different vitamins should therefore not be pooled into a single group of “vitamins and analogues”, but they should be analyzed separately. The point estimates also suggest that there is greater justification for further research on vitamin E than on vitamin C. Furthermore, vitamins E and C may also interact under some conditions; for example, Hemilä H, 2009 found that vitamin E decreased mortality of older males only when they had a high vitamin C intake, but vitamin E had no effect when vitamin C intake was low.

Finally, Su X, 2017 estimated the effect of “vitamins and analogues” on the OR scale. However, Altman DG, 1998 pointed out that OR should be avoided when events are common. In many CIAKI studies, the proportion of CIAKI cases has been so high that OR gives an exaggerated impression of treatment effect. Su et al. calculated that high-dose statin plus NAC decreased the risk of CIAKI by OR = 0.31 (95%CI 0.14-0.60) and they concluded that “high-dose statin plus NAC or high-dose statin alone were likely to be ranked the best or the second best for preventing CIAKI”. However, the upper 95%CI limit for the effect of vitamin E on the OR scale (0.58) is lower than the upper 95%CI limit for the effect of high-dose statin plus NAC (0.60). Thus, on the basis of trials published so far. there is no basis to consider that these treatments actually differ in efficacy. Furthermore, half of the patients of the three vitamin E trials were concomitantly administered statins, and thus the effect of vitamin E may be at least partly independent of the effects of statins.

Thus, had Su X, 2017 analyzed the vitamin E trials separately, they might have concluded that there is as strong evidence to further study vitamin E as to further study high-dose statin plus NAC.

On 2016 Nov 07, Cicely Saunders Institute Journal Club commented:

The Cicely Saunders Institute journal club discussed this paper on 02/11/2016

The need to address early rehabilitation in individuals with critical illness is an important clinical priority. In meeting the needs of this group, clinicians need to consider who is likely to benefit and to what extent, it is also important to address possible harms that may arise from intervention (see AVERT, Lancet 2015). This paper addresses an important area of practice in the surgical intensive care environment.

We valued our discussion of the paper, which generated a number of reflections on the methods used and the wider applicability of the intervention. In rehabilitation and palliative care practice goal-setting to target intervention is a widely used approach. In many rehabilitation contexts, goals are set in conjunction with patients, carers and the clinical team. The method used here was somewhat different and used the Surgical ICU Optimal Mobilisation Score (SOMS), which in our view was more akin to a protocol. Nevertheless, the SOMS facilitated targeting of intervention at the individual ability level and seemed appropriate to the ICU environment, where patient engagement in goal setting maybe less practical in some instances.

We noted that a significant difference was identified in delirium-free days in favour of the experimental group and that the mean difference was three days. We wondered if the authors had any further comment on this and its relationship to the beneficial outcomes identified, particularly reduced length of stay. We reflected that reduced delirium may result in improved ability to engage in rehabilitation practice.

Commentary by Lucy Fettes & Stephen Ashford

On 2016 Oct 14, Attila Csordas commented:

Authors finish the article with the following suggestion: "To further extend human lifespan beyond the limits set by these longevity-assurance systems would require interventions beyond improving health span, some of which are currently under investigation (15). Although there is no scientific reason why such efforts could not be successful, the possibility is essentially constrained by the myriad of genetic variants that collectively determine species-specific lifespan(16).”

Authors seem to be suggesting that all the current experimental efforts won’t be enough to increase maximum life span over a biological limit that has been reached already and overcome or counterbalance the collective effect of those “myriad of genetic variants”.

In fact, there is at least one experimental result that leaves this question definitely open, and this is the scenario of clearing-out senescent cells from the aging organism, see mouse studies summarised in http://www.nature.com/nature/journal/v530/n7589/full/nature16932.html where concerning maximum lifespan the results are mixed: “Maximum lifespan was significantly increased for mixed AP-treated males and females combined (P = 0.0295), but not for females and males individually. Maximum lifespan was not extended for C57BL/6 AP-treated animals, either combined or separately”. Indeed this is the approach taken by biotech companies like http://unitybiotechnology.com/ amongst others.

I wonder how a study, also appearing in Nature, earlier this year, February, 2016, have slipped through the attention of the authors?

The assumption of my argument is that mouse studies can be relevant for human trials. After all mice have those “myriad of genetic variants” too.

On 2016 Oct 26, Marco Lotti commented:

Please, see Video Comment at: https://youtu.be/ZJnt8wIvK14

You can find further resources at:

http://www.slideshare.net/MarcoLotti3/lotti-marco-md-the-laparoscopyenhanced-hipec-concept

http://online.liebertpub.com/doi/abs/10.1089/vor.2015.0315?journalCode=vor

http://www.journalofmas.com/article.asp?issn=0972-9941;year=2016;volume=12;issue=1;spage=86;epage=89;aulast=Lotti

On 2016 Oct 22, Marco Lotti commented:

Please, see Video Comment at:

https://youtu.be/ZJnt8wIvK14

On 2016 Oct 08, Marco Lotti commented:

Please find further resources at:

http://www.slideshare.net/MarcoLotti3/lotti-marco-md-the-laparoscopyenhanced-hipec-concept

http://online.liebertpub.com/doi/abs/10.1089/vor.2015.0315?journalCode=vor

http://www.journalofmas.com/article.asp?issn=0972-9941;year=2016;volume=12;issue=1;spage=86;epage=89;aulast=Lotti

On 2016 Oct 09, Preben Berthelsen commented:

Levosimendan for the Prevention of Acute Organ Dysfunction in Sepsis

Gordon AC et al. NEJM 2016.

A foregone conclusion - Levosimendan does not prevent organ dysfunction in sepsis – that is if you wait long enough before administering it.

Successful treatment of sepsis is based on the prompt administration of antibiotics, volume repletion and perhaps surgery.

In this RCT, levosimendan was first deployed a median of 15-16 hours after a diagnosis of sepsis had been established. In my opinion, it is very unlikely that any intervention - delayed for so many hours - will substantially influence the course of sepsis in a meaningful way.

This trial does not inform on a well-timed use of levosimendan in sepsis. Historically, however, single interventions in sepsis have a poor track record.

P.G.Berthelsen MD, MIA, DCAH. Charlottenlund, Denmark

On 2016 Oct 28, Lydia Maniatis commented:

It seems that the model being proposed by Snow et al (2016) was obsolete even as it was being constructed, as they decided to base it on assumptions of V1 neuron behavior known for decades to be invalid.

The choice is signaled by the authors when they explain in their introduction that they are going to “address primary visual cortex (V1) as a paradigmatic example and focus on orientation adaptation phenomena that are within the classical receptive field (RF).”

I think this is the only mention made in the article of the term “classical receptive field,” but it bears some elaboration.

The obsoleteness of the concept is reflected in quotes from two articles, below.

1. Graham (2011) "Beyond multiple pattern analyzers modeled as linear filters (as classical V1 simple cells): Useful additions of the last 25 years" Vision Research.

“The classical receptive field of a V1 simple cell is very small relative to the distances over which visual perception has to function. Indeed, the classical receptive field is typically composed of only a few inhibitory and excitatory sub-sections…

…non-classical responses of V1 simple cells can occur over a substantially larger area than the classical receptive field. This is one reason that non-classical receptive fields are now frequently invoked in explanations for perceptual phenomena.

…these non-classical receptive fields have been invoked to account for a number of psychophysical phenomena as well

…In addition to the possibility of non-classical suppressive (or facilitatory) effects from outside the classical receptive field, there is also a possibility that the same non-classical effects extend inside the classical receptive field. And perhaps there are different non-classical processes that exist inside the classical receptive field but not outside.”

1. Angelucci and Bullier (2003) Reaching beyond the classical receptive field of V1 neurons: horizontal or feedback axons? (Journal of Physiology)

“It is commonly assumed that the orientation-selective surround field of neurons in primary visual cortex (V1) is due to interactions provided solely by intrinsic long-range horizontal connections. We…conclude that horizontal connections are too slow and cover too little visual field to subserve all the functions of suppressive surrounds of V1 neurons in the macaque monkey. We show that the extent of visual space covered by horizontal connections corresponds to the region of low contrast summation of the receptive field center mechanism. This region encompasses the classically defined receptive field center and the proximal surround. Beyond this region, feedback connections are the most likely substrate for surround suppression. We present evidence that inactivation of higher order areas leads to a major decrease in the strength of the suppressive surround of neurons in lower order areas, supporting the hypothesis that feedback connections play a major role in center–surround interactions.”

Naturally, as the authors point out, the model can’t explain many things (that it should be able to explain):

“We have shown that our modeling approach can explain some classical adaptation effects as well as a more recent phenomenon of equalization. However, clearly the approach has limitations and does not capture the full set of phenomena for adaptation.

First, the model in its present form does not include surround influences and cannot capture disinhibition of the surround nor interesting data on facilitation and attractive shifts of tuning curves (Solomon & Kohn, 2014; Webb et al., 2005; Wissig & Kohn, 2012). It would be interesting to consider extensions of the model to capture both spatial (Coen-Cagli et al., 2012) and temporal contextual influences.”

The model is extremely involved. Evaluating it would require a significant amount of effort and time on the part of colleaugues. SInce even its authors already know its assumptions are false (i.e. lead to false predictions), why should anyone bother? Adding to a failed, ad hoc model is usually not the best way to achieve a better one.

The publication of models based on invalid assumptions and empirically falsified a priori is common in the vision literature and reflects a culture in which piecemeal, ad hoc (with respect to facts and techniques) and logically and/or empirically false models are treated as equivalent to coherent and insightful hypotheses that first have to be tested before we know they’ve failed.

The former, being much easier than the latter, overwhelmingly dominates the literature, which has become almost entirely self-referential and unprogressive, because its “theorists” don’t allow themselves to be challenged by inconvenient facts, but rather are satisfied with avoiding them, occupying themselves instead with mathematical prestidigitations.

On date unavailable, commented:

None

On 2017 Apr 24, David Eidelberg commented:

We thank Dr. Black for his interest in our work. To answer his basic questions:

1. The minimum time interval between the start of the levodopa infusion and the start of O15- water PET was 60 minutes. As detailed in the original paper by Feigin et al. (Neurology 2001; 57(11): 2083-2088), scanning under infusion commences when UPDRS motor ratings are stable within 5% on two successive examinations separated by 30 minutes. The levodopa infusion is maintained at a constant rate at that point.

2. As for the test-retest cohort, these PD subjects took their usual morning PD medications on the day of the scan. They maintained their routine antiparkinsonian medication regimen during the 8-week interval between test and retest imaging. The majority of the subjects were on daily carbidopa/levodopa, though a minority took a combination of levodopa and a dopamine agonist. Unfortunately, the exact dosing at the time of the scans (performed before 2008) is not currently available.

3. All levodopa infusion subjects reported in the study were scanned according to the protocol described in Hirano et al., J Neurosci 2008; 28(16): 4201-4209.

On 2017 Apr 08, KEVIN BLACK commented:

Authors: Please tell us the time interval between the start of the levodopa infusions and the start of the [O-15]water and FDG PET acquisitions.

Also, can you provide information about carbidopa intake on the day of the study? The supplement says only that the 8 PD test-retest subjects took "their usual morning dose of oral levodopa/carbidopa." The dose of LD and of CD is not given for those subjects. The reader is referred to the Ma et al 2007 paper, but I can't find dosing information there, either (nor how many were on CD-LD only and how many were on other dopaminergic drugs). In the infusion subjects, can you clarify whether the newly enrolled subjects had the same carbidopa dosing regimen as described in the Hirano et al 2008 methods?

On 2016 Nov 17, Jean-Jacques Letesson commented:

In the starting paragraph of the discussion the authors wrote "Metabolism and usage of erythritol are regulated by the 7.7‑kb ery operon, which consists of four genes eryA, eryB, eryC and eryD (EryA, 519 AA; EryB, 502 AA; EryC, 309 AA and EryD, 316 AA). The functions of these four proteases are similar to xylulose kinase (E. coli xylB), glycerol‑3‑phosphate"

I have two major comments on this sentences:

1- THESE GENES ARE NOT PROTEASES: ery is a kinase, eryB is a dehydrogenase, eryC an isomerase and eryD a transcriptional regulator

2- The EryABCD ery operon is by itself not sufficient to catabolize erythritol as published recently (Barbier T. et al., 2014.PNAS 111:17815–17820.) you need two more isomerase (eryH and eryI)

On 2016 Dec 14, Martine Crasnier-Mednansky commented:

In Escherichia coli, CRP stands for Cyclic AMP Receptor Protein, not Catabolite Repressor Protein. CRP is also known—and rightly so—as CAP, the Catabolite gene Activator Protein. Repression by CRP-cAMP, was recognized as early as 1972 (Prusiner S, 1972) and later on emphasized. See, for an elaborate discussion, Kolb A, 1993. In this context, the designation 'Cyclic AMP Receptor Protein' is fully appropriate and has been used preferentially over the more specific designation 'Catabolite gene Activator Protein'.

Glucose is not "a known inhibitor of CyaA activity". In fact, transport of glucose prevents activation of CyaA by a phosphorylated component of the phosphotransferase system (PTS). Such regulation is relevant to the present work because, upon glucose exhaustion (or some other PTS-transported carbon sources), there is a sharp increase in exogenous cAMP, which may act as a trigger at the onset of the infection.

On 2016 Oct 04, Peter Hajek commented:

It is misleading to classify people who tried one puff on an e-cigarette several weeks ago and never touched it again as 'current e-cigarette users'. The common practice of misreporting experimentation with e-cigarettes as 'current use' is responsible for the myth that large numbers of non-smokers are becoming daily vapers, when in fact this is extremely rare.

On 2016 Oct 05, Kausik Datta commented:

Congratulations to the authors for undertaking this informative study of physician behavior in Germany. I have a question about a study parameter: an important differentiating variable in this study seems to be the nature of the prescribed medication, pharmacological vs. phyto-pharmacological. However, the paper as published seems to lack any information on what medications the study considered pharmacological or phyto-pharmacological. It may likely be beyond the scope of this paper, but I'd like to have some information on the "phyto-pharmacological" medications prescribed by German GP-NPs evaluated in this study. May I request a pointer from the authors?

COI Disclosure: I have no direct competing interest with this study, the authors or their sponsors, but I am personally interested in science and ethnobotany, and am known to be skeptical of wide-ranging claims made by CAM practitioners.

On 2016 Oct 14, Daniel Jarosz commented:

None

On 2016 Oct 14, Daniel Jarosz commented:

We considered this possibility extensively, and expected to find it commonly. However, we did not observe a change protein levels for the hit proteins that we checked (see supplement), and it seems unlikely that such feedback mechanisms would be transmissible to other cells through protein alone, so strongly sensitive to transient inhibition, or stable over hundreds of generations, through freeze/thaw etc. Investigating whether any of the remaining phenotypic states that we did not test in this way could arise from feedback mechanisms like those described in this comment stands as a goalpost for our future studies.

On 2016 Oct 12, Peter Ellis commented:

The authors note that many of the proteins identified in this screen were transcription factors and RNA-binding proteins. The paper does not report whether they checked the mRNA and/or protein expression levels of the endogenous gene copy before and after transgenic overexpression of a given gene. In cases where a transcription factor promotes its own expression, or an RNA-binding protein promotes the translation of its own transcript, there is an obvious feedback mechanism through which the memory could be maintained.

On 2017 May 02, Lukasz Antoniewicz commented:

Thank you for your opinion.

On 2017 May 02, Zvi Herzig commented:

None of the sources with COIs relate to original data. The relevance of snus to this discussion is that it is the cleanest form of nicotine for which a wealth of long-term epidemiological evidence is available. As the American Heart Association notes Bhatnagar A, 2014:

Because most of the toxicity from cigarette smoking derives from combustion products, the health effects of smokeless tobacco could be examined to assess potential long-term adverse effects of nicotine without exposure to combustion products. Smokeless tobacco users take in as much nicotine as cigarette smokers, although not by the pulmonary route. The most extensive and rigorous epidemiological studies on smokeless tobacco use come from Scandinavia, where a large percentage of men use snus, a smokeless tobacco product that contains nicotine but relatively low levels of carcinogens and other toxins.

Rodu and Phillips do not present original data and their arguments cannot be refuted simply by citing their COIs. Similarly, Lee's meta-analyses do not present original data and are peer-reviewed. If any other meta-analysis refutes Lee's work, I'd be happy to cite it.

On 2017 May 02, Lukasz Antoniewicz commented:

As our study does not focus on snus I will not continue this debate. I do not question the scientific creditability of your citations, but I find it very interesting that among your citations some researchers clearly stated following:

Rodu B, 2015 Dr Rodu is supported by unrestricted grants from tobacco manufacturers to the University of Louisville, and by the Kentucky Research Challenge Trust Fund. Dr Phillips is partially supported by an unrestricted grant from British American Tobacco.

Lee PN, 2013 The author is a long-term consultant to the tobacco industry

Lee PN, 2009 PNL, founder of PN Lee Statistics and Computing Ltd., is an independent consultant in statistics and an advisor in the fields of epidemiology and toxicology to a number of tobacco, pharmaceutical and chemical companies.

On 2017 May 01, Zvi Herzig commented:

Snus users are exposed to equal or more more nicotine than smokers Holm H, 1992. If snus does not cause MI or stroke, this indicates that nicotine doesn't. This inference is also made by Benowitz and Burbank, as cited by Bates above.

The conclusions of the Arefalk study have been refuted by Rodu B, 2015 (see also Rodu's follow-up link).

The other possible effects of snus are unrelated to EPC mobilization. In any case, the link to type 2 diabetes is inconsistent, e.g. Rasouli B, 2017. Rodu shows that the correlation is consistent at >6 cans per week link, but "more research is needed to confirm a link" in his opinion, because of other known factors. With regards to cancers see Lee PN, 2009 Lee PN, 2013.

On 2017 Apr 28, Lukasz Antoniewicz commented:

I agree that we may speculate that nicotine mobilizes EPCs. But I do not agree on the last statement: I find it very interesting that Zvi Herzig cites studies on the tobacco product called snus and equates it to pure nicotine. As a tobacco product, Swedish snus is not comparable to pure nicotine. Swedish snus increases the risk for type 2 diabetes Carlsson S, 2017 and pancreatic cancer Luo J, 2007 and seems even to increase the risk for other types of cancer Zendehdel K, 2008, Song Z, 2010, Hirsch JM, 2012, Nordenvall C, 2013. As cited by Zvi Herzig, case fatality was increased among patients with myocardial infarction and stroke. This was confirmed by Arefalk, wo observed a 50% mortality reduction upon snus-cessation following myocardial infarction Arefalk G, 2014. In conclusion: Swedish snus is not the same thing as pure nicotine or a NRT. Swedish snus is probably not as safe as suggested by the comment of Zvi Herzig.

On 2017 Apr 25, Zvi Herzig commented:

Farsalinos and Polosa explicitly write:

Obviously, we are not implying that the elevation in EPCs that follows acute exposure to nicotine-containing e-cigarette reported by Antoniewicz et al. is beneficial to cardiovascular health.

Rather, they show that EPC mobilization doesn't indicate cardiovascular harm, as it occurs with activities known to be safe. Moreover, they note:

acute effects on EPC number could be related to a documented direct effect of nicotine.

See also Heeschen C, 2006:

Administration of nicotine increased markers of EPC mobilization.

Thus, the findings of the Antoniewicz el al appear to be a function of nicotine. Decades of epidemiological evidence don't indicate that nicotine causes myocardial infarction Hansson J, 2012 or stroke Hansson J, 2014, even though there might be some detrimental effects, as noted above.

On 2017 Apr 24, Lukasz Antoniewicz commented:

A lot of reviews explain the function of endothelial progenitor cells (EPCs). I will repeat some key points from our letter (https://www.ncbi.nlm.nih.gov/pubmed/28159320): EPCs are cells that participate in vascular repair. The trigger that releases EPCs from a pool into the blood stream is hypoxia in the vascular wall. This fact is well described in plenty reviews and studies. We know that smoking a single cigarette causes a sudden mobilization of EPCs, but this effect is temporary and EPCs return to baseline values during 24 hours (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3938677/). If the vasculature is exposed to chronic stress (like in the case of daily cigarette smoking) this causes frequent releases of EPCs into the blood stream resulting in a diminished pool of EPCs. So, when analyzing EPCs in chronic smokers (but not directly after smoking a cigarette) the amount of EPCs is lower compared to non-smokers. Upon smoking cessation, this pool seems to be replenished and the amount of EPCs increases. The cited studies investigating the effects of red-wine consumption or Mediterranean diet investigate the pool of EPCs in a ”steady state” so the terms long-term and short-term are relative. We investigated the sudden effects (during hours) on EPC-release following smoking and e-cigarette inhalation.

Physical activity causes physiological stress on muscles and vessels resulting in physiological hypoxia causing a sudden mobilization of EPCs following only hours of physical activity. It is important to highlight that this mobilization is triggered as a physiological response following exercise. It is hard to argue that smoking a couple of cigarettes a day with several EPC releases has a beneficial effect on health.

Our study shows that e-cigarette inhalation has the potential to mobilize EPCs that are needed for vascular repair. We will see if daily mobilization diminishes the pool of EPCs. It remains to be shown if daily e-cigarette inhalation causes chronic changes to the vascular wall. Maybe in 20 or 30 years we will get a clear answer if the number of e-cigarette users continues to increase and epidemiological studies on myocardial infarction and stroke will give us more information. Until then, there will be a lively debate.

On 2016 Dec 23, Clive Bates commented:

In their published reply to this article, Endothelial progenitor cell release is usually considered a beneficial effect: Problems in interpreting the acute effects of e-cigarette use, Farsalinos and Polosa point out that the measured increase in endothelial progenitor cells (EPCs) is usually associated with beneficial effects, and not necessarily a cause for the concerns expressed by the authors.

Farsalinos and Polosa point out that several problem conditions are associated with lower EPC levels:

However, the increase in EPC levels is largely interpreted in the scientific literature as a beneficial effect while a reduction is interpreted as an adverse prognostic marker. Several risk factors for cardiovascular disease, such as ageing, hyperlipidemia, hypertension, obesity and diabetes, are associated with reduced levels and functional impairment of EPCs. Similar associations were found with “non-classic” risk factors such as high C-reactive protein and homocysteine, and low vitamin D levels. Smokers have lower levels of EPCs compared to nonsmokers.

They also point out that many positive conditions are associated with higher EPCs:

Various short-term or acute interventions are associated with elevated EPCs. Consumption of red wine, switching to Mediterranean diet and acute exercise are associated with elevated number of circulating EPCs in healthy subjects. EPCs increase shortly after smoking cessation (especially in light smokers), with nicotine patch users having slightly higher (but not statistically significant) elevation in EPCs after smoking cessation compared to non-users. Short-term administration of green tea also caused an increase in EPCs in young healthy smokers. In all the above-mentioned interventions, the increase in EPCs was interpreted as a beneficial effect and there was no suggestion that it was a response to vascular injury caused by the intervention

This is merely the latest of several recent analyses in which observations of acute effects of nicotine have been uncritically assumed to be a marker for a chronic cardiovascular disease risk (see Vlachopoulos C, 2016 and Carnevale R, 2016 for example), generating alarming news headlines as a result (see: E-cigs: The incendiary truth... Just 10 puffs increases your risk of heart disease, Daily Mail, 3 Dec 2016).

Please see 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.

The absence of serious disease risk when nicotine is consumed through NRT or smokeless tobacco (i.e. without the products of combustion of tobacco leaf) should be a basis for reassuring and encouraging smokers considering switching to vaping.

I hope the authors and journal will take care that any misunderstandings generated by their work and the media attention that followed will be corrected and placed in context. The problem is that alarming but baseless statements about vaping risks can easily have the unintended effect of encouraging continued smoking and cause harm as a result.

On 2017 Aug 11, Jos Verbeek commented:

Unfortunately this review did not adhere to the following important Cochrane standards. There was no published protocol. The authors combined the results of all RCTs and case series thus artificially inflating the effect. They pooled very different interventions in one pooled result even though heterogeneity was as high as 82%. I believe that calculating one pooled effect size for interventions as different as meditation, communication skills or improved work schedules does not make sense. It is also not a methodological standard to loosely asses the quality of the evidence as moderate without further justification and not using the GRADE approach. Another interesting item is the claim that the results are ‘clinical meaningful reductions’. It is not clear what the authors refer to. With patient-reported outcomes one would be interested in a minimally clinically relevant difference or reductions that patients perceive as an improvement. However, for the Maslach Burnout Inventory this difference has never been established as far as we know. Thus we don’t know what the clinical meaning of reductions on this scale is. It is very well conceivable that these will not be perceived as improvements by an individual health care worker. West et al neither discuss the problem of small studies that is apparent with the average number of participants being less than 50 in the 15 included trials but again loosely refer to the funnel plot as not indicating publication bias. I believe that physicians are put on the wrong foot with the conclusion of moderate quality evidence of clinically meaningful reductions in burnout based on this review.

On 2016 Oct 08, Lydia Maniatis commented:

The authors state in their conclusion that: "At each contrast level, the perceived depth first increases with the magnitude of disparity modulation up to a critical value and then decreases gradually with further increases in the magnitude of disparity modulation. "

As is well-known, perceived depth is largely mediated by stimulus structure. The stimuli used by Chen et al (2016) have a structure that produces a 3D impression. Do the "single-cycle" and the "corrugated" version, produce the same depth impression as forms, i.e. viewed in outline monocularly? Then this would have to be factored in to the conclusions re disparity and contrast. Are the authors claiming that they have controlled for this factor? Then this should be stated. Otherwise, their results can only be said to hold for the particular stimuli they employed, not for perception in general. In this case, there are no principles being investigated here; results have no predictive value; conclusions are purely ad hoc.

The most simple illustration of the role of luminance structure (combined with the principles instantiated in the visual system) is what happens in a completely homogeneous visual field, produced by a flat surface - in other words one with zero contrast. In this case, we perceive a cloudy, 3D space. A small luminance variation on that surface collapses the perceived fog into a flat perceived surface. If we converted that surface into an image that we would refer to as trompe l'oeil, we would have a very strong impression of 3D structure with zero disparity. At low contrast or high contrast, if structure implies depth, we'll see depth, and vice versa.

With respect to subjects, as is very common in psychophysics, there were very few - three here - and one of them was an author. The participation of authors is odd especially in light of the fact that we're told explicitly that the other two subjects were "naive to the purpose of this study." If it's important that the observers be naive, then why is an author a subject; if it's not important, why mention it?

Other points: The authors fail to consider the distinction between luminance contrast and perceived constrast. They modulate the luminance contrast between dots and background. We know that small elements, like thin lines, tend to produce assimilation with the background, i.e. lowers perceived contrast.

The authors mention that previous studies, using various stimuli and conditions, have produced inconsistent results. Despite these studies, we're told, " it is still difficult to infer the effect of luminance contrast effect on perceived depth in a scene..." So the question the authors seem to be asking is "what is the effect of luminance contrast on perceived depth in a scene?" But if the previous studies show anything, it is that conditions matter; so a search for "the effect" seems inappropriate. Picking a set of conditions out of a hat and testing them will only tell us about the luminance contrast effect under those conditions. The set of possible conditions is infinite.

The authors state in their intro that "as shown in signal detection theory (Green & Swets, 1966; Chen & Tyler, 2001), the threshold measurement constituting stereoacuity depends not only on the intensity of the stimulus but also on the internal noise." Neither Green & Swets (1966) nor Chen & Tyler (2001) have shown that there is noise in the visual system, and they have certainly not shown that this putative internal noise is maintained and expressed in the percept. The "internal noise" claim has generated no evidence (it is not even clear what this evidence would look like, including in terms of physiological measurements), and is maintained on the basis of studies employing a narrow set of conditions generating crude datasets whose results are highly overinterpreted.

On 2016 Oct 11, Lydia Maniatis commented:

The authors of this study transparently misrepresent and/or misunderstand the theoretical situation with respect to the subject they are investigating.

The most blatant oversight involves the failure to note that the type of stimulus being used here – a checkerboard configuration – was shown decades ago to reduce, rather than enhance, perceived contrast in adjacent surfaces. (see demo here: https://www.researchgate.net/figure/225158523_fig5_Fig-5-The-DeValois-and-DeValois-Checkerboard-stimulus). This fact was similarly overlooked by Maertens, Wichmann and Shapely (2015), who simply assumed the opposite.

The checkerboard configuration is clearly a special and unusual case, in the sense that it elicits the impression of adjacent surfaces rather the more typical experience of surfaces on top of backgrounds (figure/ground relationships). It is unlikely that an ad hoc model that involves averaging of luminances would work for both the former and the latter sets of conditions.*

The Missing Segmentation Step

In general, Wiebel et al (2016) have chosen not to address the fundamental factor mediating color and lightness, i.e the structure of the stimulus and the principles by which the visual system organizes the retinal projection to form the percept. Yet Zeiner and Maertens (2014), whose “normalized contrast model” the authors are applying here, acknowledged this gap in retrospect:

“The important piece of information that is still missing, and which we secretly inserted, was the knowledge about regions of different contrast range. Here we simply used the values that we knew to originate from the checks within the regions corresponding to plain view, shadow, or transparent media, but for a model to be applicable to any image this segmentation step still needs to be elucidated.”

But the entire problem - the ability to predict perceived lightness of any surface - lies precisely in the "segmentation step." Furthermore, since they haven't taken connection of structure to assimilation and contrast into account, it is, as noted above, doubtful that their model would work in general, even if they were to similarly sneak segmentation in through the back door.

Wiebel, Singh and Maertens sidestep the issue, simply assuming “that the visual system is sensitive to differences in contrast range and can use them to detect regions seen in plain view, because they have the highest contrast range.”

The problem, of course, is that the contrast ranges of different “regions” of an image depend on how the image is divided up in the perceptual process; again, they depend on the “segmentation step” that Wiebel, Singh and Maertens, like Zeiner and Maertens, (2016) sneak in unanalyzed.

The failure to address structure and principles of organization is also reflected in the fact that their definition of contrast depends on comparing luminances in an arbitrary, local area of the total image, rather than everything the observer could see, both on and off the screen. Again, the consequences of this global image depend on the “segmentation” step.

Model Failures Can't Be Redeemed By Ad Hoc Successes

The “model” the authors leave us with is not only ad hoc, it fails tests within this study. The abstract indicates the Zeiner Maertens model model fails even for the narrow (and very unusual) set of conditions chosen, but that “model extensions” “fit the observed data well.” In the discussion we find that the fits weren’t all that good: “For the normalized contrast model, significant differences between model predictions and observed data were shown for Reflectance 6 (p < 0.05) in the light transparency. For the dark transparency, significant differences were found for Reflectances 3, 5, 6, 8, and 9 (p < 0.05).” In other words, even for the highly selective conditions used, fits were hit-and-miss. The authors don’t have the theoretical tools to explain why (though the tools are arguably available). But they speculate, and make the following very odd statement.

In contrasting their “normalized contrast model” with the “contrast ratio model,” they note that one works for better for the “light transparency” conditions and the other for the “dark transparency” conditions. This, they argue, is due to the anchoring assumptions of each model. They propose to create new stimuli to “decide between the two models.”

But each of the models has already failed. These failures won’t be undone by any future “successes.” Any such successes would obviously be ad hoc, another theoretically and factually agnostic exercise such as the one we are discussing. No amount of such structure-blind, ad hoc model-building could take us even to the point of knowledge already available, though ignored.

Short Summary: 1. The authors construct ad hoc models of lightness perception without taking into account the fundamental mediator of lightness, i.e. stimulus structure and the principles by which the visual system organizes the retinal projection.

1. Their model fails a number of tests in this study, but they propose to keep on testing it, in order to “decide” between it and an alternative, which has also failed a number of the tests put to it in this study.

It is not clear what is the purpose in testing two failed, ad hoc models. Clearly, they are both capable of “succeeding” and of failing in an infinite number of cases.

*The assimilation that we see in the checkerboard demo is linked to the fact that contrast enhancement is highly correlated with perceived figure ground relationships, making the borders of the figure more visually salient. Percieved figure-ground relationships in turn hinge on conditions indicating figural overlap, such as intersecting continuous edges of potentially closed figures. In the case of the checkerboard, the perceptual relationships between squares is one of adjacency rather than overlap. Luminance changes interpreted as occurring within a single surface tend to produce assimilation, as for example in the case of the Koffka ring.

On 2017 Jun 14, C Trolle commented:

DNAmethylation and RNAseq data from out Turner study has finally been released.

https://www.ebi.ac.uk/ega/studies/EGAS00001002190

On 2016 Sep 30, Clive Bates commented:

There is nothing at all in these findings to justify the conclusion. In fact, the findings are more likely to support the opposite - that such social media activity is helpful in reducing smoking. If vaping companies are "enticing consumers" it is almost always to stop smoking and to vape instead. So if these tweets were actually affecting behaviour, it is likely that it would be in a way that reduces smoking and is beneficial to public health.

The authors cannot know if these tweets do actually cause changes in smoking or vaping status. However, it seems likely (by which I mean 'obvious') that vaping-related tweets would be seen by almost exclusively people who already vape. The key design feature of twitter is that users opt into the content they wish to see by choosing to follow other users. Non-vapers are unlikely to follow a vaping company or vaping review feed. Equally, advertising is targeted at users algorithmically to reach users and potential users )i.e. smokers). So the likelihood is that, if these tweets have any impact at all, it will be in shaping preferences among those already vaping for particular flavours, brand or retailers or advertising an alternative to smoking, albeit one that the authors appear to disapprove of.

The authors seem concerned that only 3% mention vaping as a way of quitting smoking. Why should that matter at all? If people are attracted to vaping for different reasons but give up smoking as a result, what's the problem? Furthermore, The Vaper points claims about quitting smoking are usually banned or deemed irresponsible Kavuluru R, 2016. Other authors have managed to be worried about the finding the opposite van der Tempel J, 2016.

There is no justification for doing this work in the first place, no case to publish such flawed interpretation of the findings, and no need to spend any time or money following its self-evidently false conclusion and inappropriate policy recommendation.

Disclosure: 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 Nov 07, John Sotos commented:

In assessing the possible impact of machine learning on clinical medicine, Obermeyer and Emanuel(1) describe the narrowing gap between human vs. computer analysis of images, and declare that "machine learning will displace much of the work of radiologists and anatomical pathologists."

We hesitate to agree, owing to the Jevons paradox and elastic demand for medical imaging.

In 1865, the economist William Jevons predicted that more efficient coal-burning in manufacturing plants would not lower the nationwide consumption of coal. Instead, the lower cost per unit of energy would increase demand for coal energy and thereby increase consumption(2).

Thus, assuming machine interpretation lowers the cost per imaging study, future human case loads will depend on the quantitative balance between a Jevonsonian increase in imaging (if any(3)) and the fraction of cases where computers completely exclude humans (e.g. only 25% for contemporary computerized Pap smear interpretation(4)).

Clearly, major changes are coming, but, given healthcare's tangled economics, it is premature to affirm that computerized image interpretation will decimate physician workloads.

John Sotos, MD

Lester Russell, BM DRCOG MRCGP MBA

(1) Obermeyer Z, Emanuel EJ. Predicting the future -- big data, machine learning, and clinical medicine. N Engl J Med. 2016; 375: 1216-1219.

(2) Jevons WS. The Coal Question. London: Macmillan and Co., 1865. Pages 102-104.

(3) Polimeni JM, Mayumi K, Giampetro M, Alcott B. The Jevons Paradox and the Myth of Resource Efficiency Improvements. New York: Earthscan Routledge, 2008.

(4) Bengtsson E, Malm P. Screening for cervical cancer using automated analysis of Pap-smears. Computational and Mathematical Methods in Medicine. 2014; Article ID 842037. http://dx.doi.org/10.1155/2014/842037

On 2016 Nov 10, Øjvind Lidegaard commented:

Thanks to Chelsea Polis for her interest in and comments on our study.

First, the group of non-users, which was the reference group in the main analysis, includes those users of copper IUD which Chelsea Polis calls for, in addition to users of barrier methods, eventually combined with natural methods such as interrupted coitus or calendar methods. The important point here is, that those women who previously have used or in the future will use hormonal contraception are among those women. Therefore, it is not correct to consider the control group as a group of women not using contraceptive methods.

Our recommendation of further studies on this issue was not primarily due to uncertainty about the methods or the results we achieved, but more the fact that sometimes scepticism is easier to overcome when several study groups reach the same results as achieved in one sound large cohort study as the Danish study.

We also made assessments including pregnant women. For all users of oral contraceptives the relative risk of first antidepressant use actually increased with inclusion of pregnant and delivering women from 1.23 (1.22-1.25) to 1.31 (1.29-1.32) and for the 15-19 year old users the relative risk of antidepressant use was unchanged 1.8 (1.75-1.84). The increase is due to those women who begin taking oral contraceptives within the first six months after delivery, and who already have an increased risk of depression due to their delivery.

In Denmark 4% of women of reproductive age are pregnant, while 40% are current users of some kind of hormonal contraception. That is another good reason why the inclusion of pregnant women does not have much impact on the risk of depression in users of hormonal contraception. And remember that the majority of delivering women get pregnant because they want to, and not because of contraceptive failure. Women getting unwanted pregnant and choose to terminate their pregnancy, generally do not get depressed, which was demonstrated in another large Danish prospective study (1), despite the frequent claim of the opposite from especially opponents of legal abortions.

The biggest weakness of our study is in our opinion the comparison group of non-users in the main analysis. A more correct comparison group would have been never-users. The influence of hormonal contraception on depression risk increases from 1.2 to 1.7 with this change in comparison group. So if anything, our relative risk figures are underestimated.

1. Munk-Olsen T, Laursen TM, Pedersen CB, Lidegaard Ø, Mortensen PB. Induced first-trimester abortion and risk of mental disorder. NEJM 2011; 364; 332-9.

On 2016 Nov 07, Chelsea Polis commented:

This analysis by Skovlund et al. (1) suggests that Danish women who currently or recently used various types of hormonal contraception may be at greater risk of being diagnosed with depression or initiating use of antidepressants, as compared against those who formerly or never used hormonal contraception. As the authors conclude, this study suggests that “further studies are warranted to examine depression as a potential adverse effect of hormonal contraceptive use”. This is particularly important since the study was unable to provide information on these outcomes among women using non-hormonal contraceptive methods, such as a copper IUD, which may have helped to clarify whether the observed associations were related to factors common to women choosing to use contraception, or to the hormonal content of the methods assessed.

Importantly, the investigators note that they censored person-time during pregnancy and through six months post-partum. The authors characterize this as a strength of the study, noting that it was done to reduce the influence of postpartum depression on the results. However, women not using highly effective methods of contraception are presumably more likely to become unintentionally pregnant, which also has implications for women’s mental health. (2)

A sensitivity analysis not excluding pregnant and post-partum person-time could be useful in better understanding the potential competing risks faced by women in their day-to-day lives. It would be helpful for the authors to present pregnancy rates by contraceptive status, and to replicate the main analyses without excluding pregnant and post-partum person-time.

Sincerely,

Chelsea B. Polis, PhD, Senior Research Scientist, Guttmacher Institute

Ruth B. Merkatz, PhD, RN, FAAN, Director, Population Council

1. Skovlund CW, Mørch LS, Kessing LV, Lidegaard Ø. Association of hormonal contraception with depression. JAMA Psychiatry 2016 (Epub ahead of print).
2. Abajobir AA, Maravilla JC, Alati R, Najman JM. A systematic review and meta-analysis of the association between unintended pregnancy and perinatal depression. J Affect Disord 2016;192:56-63.

On 2016 Oct 04, Quinn Capers commented:

Thank you for your interest in our work. Briefly, we are aware of theories that the IAT may measure something other than racial bias. However, regardless of what they are actually measuring, IAT results predict discriminatory behavior. Secondly, it was beyond the scope of the paper to control for the Hawthorne effect, but we acknowledge that behaviors could have changed because committee members were aware that they were being observed. Finally, we agree that an analysis of the composition of the class following the IAT should be accompanied by full admissions statistics pre- and post- the exercise. This is provided in the paper and commented on (Table 2). Word count restrictions prevented us from including this information in the abstract. Feel free to email me after reading the full length paper.

On 2016 Sep 30, Thomas Heston commented:

Does the black-white implicit association test measures racial bias? Or something else? (Kaufman SB. Psych Today 28-Jan-2011 https://goo.gl/h3jvw1). Suffice it to say that there does exist at least some controversy. The authors also failed to control for the Hawthorne Effect (BMJ 2015;351:h4672 http://bit.ly/2dqvD4p). The statement that the class that matriculated following the IAT exercise was the most diverse is really meaningless without examining the applicant pool. Examine bias? Yes, by all means. But don't ignore potential test bias and researcher bias which may make the results unscientific.

On 2017 Oct 26, Martine Crasnier-Mednansky commented:

This paper reinforces –perhaps validates– the authors’ previous work (Mondal M, 2014) indicating PTS-transported GlcNAc is utilized by Vibrio cholerae in the mucus layer, as further explained.

Data in Meibom KL, 2004, particularly supplemental figure 7, clearly indicate chiA2 (VCA0027) is not upregulated by GlcNAc. Therefore, in agreement with the present work, GlcNAc utilization by V. cholerae in the mucus may rely on the periplasmic activation of ChiS for production of ChiA2. Because chiS mutant strains do not produce extracellular chitinases in the presence of chitin oligomers (Li X, 2004), they are unlikely to produce chitinases in the presence of mucin (the authors report ChiS is activated in the presence of mucin). Thus, both chiA2 and chiS mutant strains may prevent colonization of the intestine because they are both unable to cause mucin hydrolysis by ChiA2 and subsequent release of GlcNAc, which, according to the authors’ original 2014 proposal, is necessary for growth and survival in the mucus. The mucin-derived 'inducer' for ChiS activation is possibly (GlcNAc)3, as the authors reported (GlcNAc)3 is released upon mucin hydrolysis by ChiA2.

On 2016 Sep 28, Jonathan Eisen commented:

A preprint of this paper is available at BioRXiv: http://biorxiv.org/content/early/2016/08/25/071548

On 2017 Jun 12, Maria Sammartino commented:

"The interaction of the electron beam, emitted by the gun, with the sample induces an excitation, energy is lost and a single X-ray is emitted that is characteristic of the element hit." A very bad description of the EDS! Anyway the author Gatti A.M. improved her knowledge on the subject; really in one of her oldest article ( Liver and kidney foreign bodies granulomatosis in a patient with malocclusion, bruxism, and worn dental prostheses.By: Ballestri, M; Baraldi, A; Gatti, AM; et al. GASTROENTEROLOGY Volume: 121 Issue: 5 Pages: 1234-1238 Published: NOV 2001)she defined the X-ray microprobe "radiograph microprobe" May be due to the scarce knowlege of the EDS mechanism, that imply an elemental analysis, the error usual in almost all the articles by Gatti is to state that what she find in the sample are non-biodegradable metals (The particles detected showed to contain highly-reactive, non-biocompatible and non-biodegradable metals. It is not specified to which of the white particles the spectra in fig. 1 refer. In my opinion, from the SEM images of the same figure, i.e. at such magnitude, it is almost impossible to measure the particles dimension. Further, even if the total surface occupied by the sample on the acetate filter is not declared, in my opinion, it is anyway almost impossible to count all the particles in a reasonable time; as an example the SEM image show an area of about 50x50 micrometers; how many images they have to acquire to cover a 10x10 mm area? The PCA is at all not explained, and not correctly graphicated. First of all the graph of the two Principal Components must be isometric and squared; the graph of the Loadings lacks and, looking at the data reported in tables and hystogram, it is unclear what they are; the first two components account for less than 47% of the total variance and the graph of the % variance as a function of the components lacks

On 2017 Feb 01, Davide Radice commented:

Visani G et al, compared the occurrence of nanoparticles and aggregates in the peripheral blood samples of AML patients and healthy subjects in a matched case-control study and based on their findings they argue that nanoparticles could lead to AML (that is: nanoparticles could be a risk factor for AML). However I found a number of issues regarding both the design and the statistical analysis. Here in brief the most relevant ones:

1. apart from the few number of subjects included they say that AML patients were matched with healthy subjects, however they do not specify which confounders they matched and controlled for (Table 1 only describes the characteristics of the AML patients but not those of the matched healthy subjects)

2. the primary analysis compares the average particles and aggregates counts, element by element (Table 4) through a series of two-sample t-tests: it should be kept in mind that

   a) the t-test is not suitable for count data because counts violate the underlying assumptions, thus any inference based on the significance of the t-test must be considered as possibly wrong

   b) despite they call each t-test as ‘independent’ because they consider controls as independent of cases, the individual tests are not independent of one another due to the fact that they all were conducted on the same sample of subjects. This is a well-known additional issue called ‘the multiple comparison problem’ they would have to take into account even if they used a more appropriate non-parametric alternative to the t-test. For example taking the 19 raw p-values in Table 4 it can be shown that after adjusting for the multiplicity using the Holm method [1], the only statistically significant comparisons are those regarding the average counts for Al (p = 0.019) and Ca (p = 0.019).

Moreover a statistically significant difference for the average of the counts between AML and healthy subjects it does not imply that aggregates and particles can be considered as possible risk factors, as can not be inferred in general as a risk factor any other variable just on the basis of the significance of the difference between two means (think for a while to a significant difference between the average shoes size, observed by chance). To conclude correctly about a risk you don’t compare two means, you must estimate and test the risks. The authors they should have properly analyze their data using a conditional logistic regression model [2]

Taking the data in Table 2 and assuming that each sample in a row shows the counts of a properly matched case-control for the unspecified confounders, I ran the appropriate statistical analysis (SAS 9.3) as described above. Taking the controls as reference the (multivariable) conditional logistic regression analysis clearly shows that neither aggregates nor particles are significant risk factors for AML. Here the results:

• particles : OR = 1.19 (95% CI: 0.83,1.69) p = 0.34
• aggregates: OR = 0.58 (95% CI: 0.09,3.83) p = 0.57

Legenda: OR = Odds Ratio, CI = Confidence Interval

[1] Holm, S. (1979). "A simple sequentially rejective multiple test procedure". Scandinavian Journal of Statistics. 6 (2): 65–70

[2] Breslow, N. E., et al. (1978). "Estimation of multiple relative risk functions in matched case-control studies.". American Journal of Epidemiology. 108 (4): 299–307

On 2016 Nov 16, Joe G. Gitchell commented:

Readers may find my post and the subsequent discussion of interest at this link (which includes relevant disclosures): http://conscienhealth.org/2016/11/finding-a-way-for-healthier-generations/

On 2016 Sep 29, Andrew Brown commented:

The ability to evaluate and compare this study is limited by missing methodoligical details about the outcome phenotype: various measurements of obesity and adiposity. Please excuse me if I missed the details somehow, and I hope the authors will consider adding details to better help the scientific community evaluate the authors' contribution to microbiome-obesity research.

The authors state that they evaluated three measures of abdominal adiposity, inlcuding subcutaneous fat mass (SFM). SFM is not a measurement of abdominal adiposity unless restricted to the abdomen. The methods do not make such a distinction, and instead only indicate the data were collected from DXA. The authors cite two articles in the methods with respect to adiposity phenotypes; neither describe how SFM was defined.

The authors state, "Visceral fat mass was calculated from one cross section of the whole body at L4–L5, the typical location of a CT slice;" no reference is provided to defend the reliability or appropriateness of such a method. For instance, some methods have used different lumbar positions and some people insist that DXA is inappropriate for visceral adipose tissue estimation.

The authors also dichotomize 'high' and 'low' phenotypes of adiposity measurements without explanation in Figure 2. The methods of dichotomizing also are not clear: "For each phenotype, individuals who were more than 1.5 standard deviations from the mean of the phenotype were assigned to high and low phenotype groups respectively." Does this mean those less than 1.5 SD below the mean were 'low' and those more than 1.5 SD were 'high'? This would eliminate a large portion of the sample (+/- 1.5 SD removed from the middle of the distribution would leave <15% of the sample if it was normally distributed). If, on the other hand, it was dichotomized on a single point value 1.5 SD above the mean (for instance), this has severe limitations because such cutoffs can be slid along the continuum to provide very different results. Thus, it is typically best to provide a theoretical basis for classification or to have a confirmation set (e.g., see Ivanescu AE, 2016).

It is also unclear if these dichotomized values were used throughout the rest of the manuscript (e.g., they appear to be in figure 4). This impairs the reader's ability to evaluate results and compare to new or old findings.

On 2016 Oct 24, Sean Ekins commented:

here are infographics http://www.slideshare.net/ekinssean/tb-infographic-euro-funding http://www.slideshare.net/ekinssean/tb-infographic

On 2016 Dec 05, Donald Forsdyke commented:

SELECTIVE PRESSURE TO CONSERVE VIRUS SPECIES IDENTITY

The authors correctly note that "the most obvious parameter associated with G + C content is the strength of molecular hybridization of polynucleotide duplexes" (1). Such hybridization controls recombination, which is favored when there is close sequence resemblance between different co-infecting viruses ("complete alignment conserved"), and is impeded when there is less sequence resemblance ("complete alignment variable"). The latter anti-recombination activity can be considered in relation to speciation mechanisms that initiate and retain taxonomic differentiations. As recently noted by Meyer et al., allied species of "viruses that infect the same [host] species and cell types are thought to have evolved mechanisms to limit recombination." Without such limitations the genomes would blend and co-infectants would lose their independence as distinct viral species. Mechanisms overcoming this selective disadvantage include "divergences in nucleotide composition and RNA structure that are analogous to pre-zygotic barriers in plants and animals" (2).

Thus, a nucleic acid region may be "conserved," not only because it encodes a protein (i.e. there is "protein pressure" on the sequence), but because it has a specific nucleotide composition (e.g. "GC-pressure"). While protein pressure mainly affects the first and second codon positions, GC-pressure can affect all codon positions. Indeed, at first and second codon positions there may be conflict between pressures, especially when protein pressure is high (i.e. in regions where amino acid conservation is high); then GC-pressure is constrained to vary only at the more flexible third codon position. In contrast, when protein pressure is low (i.e. in regions where amino acid conservation is low), then GC-pressure has greater freedom to affect all codon positions.

If, to avoid recombination, there is selective pressure on one branch of a diverging line to decrease its GC%, then it would be predicted that "the GC% of nucleotides encoding conserved amino acid (AA) residues" would be "consistently higher than that of nucleotides encoding variable AAs," where the pressure to decrease GC% has fuller rein to encompass all three codon positions (1). Conversely, it would be predicted that when there is pressure on a diverging line to increase GC%, then it would be predicted that the GC% corresponding to conserved codons would be consistently lower than that of non-conserved codons (e.g. Ebolavirus).

For flavivirus "the mean G% of the core conserved AA residues is higher (35%) than that of the variable AA residues (28%), but the mean G3% of the core conserved AA residues (28%) is similar to that of the variable AA residues (29%)" (1). While consistent with the above views, there is need for information on C3% and relative frequencies of synonymous codons (e.g. the two cysteine codons correspond either to low or high GC%). More details of selective anti-recombination pressures are presented elsewhere (3, 4). Similar considerations may apply to codon biases and GC% among mycobacteriophages (5).

1.Klitting R, Gould EA & de Lamballerie X (2016) G + C content differs in conserved and variable amino acid residues of flaviviruses and other evolutionary groups. Infection, Genetics and Evolution 45: 332-340.Klitting R, 2016

2.Meyer JR, Dobias DT, Medina SJ, Servilio L, Gupta A, Lenski RE (2016) Ecological speciation of bacteriophage lambda in allopatry and sympatry. Science 354: 1301-1304. Meyer JR, 2016

3.Forsdyke (2014) Implications of HIV RNA structure for recombination, speciation, and the neutralism-selectionism controversy. Microbes & Infect16:96-103. Forsdyke DR, 2014

4.Forsdyke DR (2016) Evolutionary Bioinformatics, 3rd edition. Springer, New York.

5.Esposito LA, Gupta S, Streiter F, Prasad A, Dennehy JJ (2016). Evolutionary interpretations of mycobacteriophage biodiversity and host-range through the analysis of codon usage bias. Microbiol Genomics 2(10), doi: 10.1099/mgen.0.000079. See arXiv preprint

On 2017 Jun 30, Seán Turner commented:

Traore et al. (2015) [PMID 27257486] and Vicino et al. (2016) [PMID 27660714] both claim DSM 29078 to be the type strain of Bacillus andreraoultii and Murdochiella massiliensis, respectively. DSM 29078 is not listed in the DSMZ online catalog of strains as of 30 June 2017.

On 2017 Feb 03, Robert Eibl commented:

Great work!

On 2016 Dec 08, Ole Jakob Storebø commented:

Spin and double spin ̶ the Letter to the Editor by Romanos et al. (2016) is indeed spinning.

Response to “Check and Double Check ̶ the Cochrane review by Storebø et al. is indeed flawed” 

(This letter was rejected by the editors in Zeitschrift für Kinder- und Jugendpsychiatrie und Psychotherapie).

Romanos et al. 2016 (Romanos M, 2016) continue to publish disagreements with the findings of our Cochrane systematic review (Storebø OJ, 2015) that do not have any meaningful effect on our estimate of effect size regarding methylphenidate for children and adolescents with ADHD. Our main point is that due to the very low quality of all the evidence one cannot state anything for sure about the true magnitude of the effect.

It is correct that a post-hoc exclusion of the four trials with co-interventions in both MPH and control groups and the one trial of preschool children will change the effect size from 0.77 to 0.89. We have responded several times to this group of authors (Storebø OJ, 2015, Storebø OJ, 2016, Storebø OJ, 2016, Storebø OJ, 2016, OJ Storebø et al, 2016: doi:10.1136/eb-2016-102499) regarding these trials which were included in keeping with our protocol which was published a priori (Storebø OJ, 2015).

We agree that there might be an effect of both Clonidine and behavioral therapy. However, the effects are balanced by their use as add-on therapies in both arms of the trials i.e. the methylphenidate and no-methylphenidate arms. Such an analysis would be a post hoc decision made purely to increase the effect size and would be in conflict with our reviewed protocol (Storebø OJ, 2015).

There is no evidence for providing a valid cut off score for the effect size of the standardized minimal clinical difference (SMD) that can be used by clinicians. When reporting a SMD one of the challenges facing researchers is to determine the significance of any differences observed and communicate this to clinicians who will apply the results of the systematic review to clinical practice.

The use of a Minimal Clinical Relevant Difference (MIREDIF) is a valid way to express the minimum clinically important improvement considered worthwhile by clinicians and patients (Copay AG, 2007). The variability of MIREDIF is also important, which is why we reported the 95% confidence intervals of the transformed mean value in our review. Even with a difference in means below the MIREDIF, a proportion of the patients will have a value above the MIREDIF. Similarly, a proportion of the patients will have a value below the MIREDIF.

The use of end-of-period data in cross-over trials is problematic due to the risk for “carry- over effect” (Cox DJ, 2008) and “unit of analysis errors” (http://www.cochrane-handbook.org.). In addition, we have tested for the risk of “carry-over effect”, by comparing trials with first period data to trials with end-of-period data in a subgroup analysis. This showed no significant subgroup difference, but this analysis has sparse data and one can therefore not rule out this risk. Even with no statistical difference in our subgroup analysis comparing parallel group trials to end-of-period data in cross-over trials, there was high heterogeneity and this could mean that the risk of “unit of analysis error” and “carry-over effect” was in fact real.

We have continued to argue that the well known adverse events of methylphenidate, such as the loss of appetite and disturbed sleep, can be detected by teachers. We highlighted this in our review (Storebø OJ, 2015) and answered this point in several replies to these authors (Storebø OJ, 2015, Storebø OJ, 2016, Storebø OJ, 2016, Storebø OJ, 2016, OJ Storebø et al, 2016: doi:10.1136/eb-2016-102499). It is not about controlling the amount of food children eat in the schoolyard or assessing their sleep quality at night. The well known adverse events of “loss of appetite” and “disturbed sleep” are easily observable by teachers as uneaten food left on lunch plates, yawning, general tiredness and even weight loss.

There is considerable evidence that trials sponsored by industry overestimate benefits and underestimate harms (Lundh A, 2012, other citations). We did receive a table for the Coghill 2013 trial from the authors. We did, however, not ask for information about funding as it was clearly stated in Coghill 2013 that this trial was funded by Shire Development LLC (Coghill D, 2013).

It is true that some participants in the MTA study (10%) allocated to the methylphenidate treatment were titrated to dextroamphetamine (Anonymous, 1999). We wanted to conduct a reanalysis of the data excluding the participants who did not receive methylphenidate. We contacted Dr. Swanson and he proved several helpful comments. He also enclosed published articles, but we did not receive additional data, in part because of the time frame of our review (Storebø OJ, 2015). Sensitivity analysis excluding the MTA study does not significantly change the effect estimate.

We have seriously considered the persistent, repeated criticisms by Ramonas et al. published in a number of different journals, however, none of these have provided evidence which justify changing our conclusions about the effects of MPH and the very low quality of evidence of methylphenidate trials. We had no preconceptions of the findings of this review and followed the published protocol, therefore any proposed manipulations of the data proposed by this group of authors would be in contradiction to the accepted methods of high quality meta-analyses. As it is unlikely that any further criticisms from these authors will change and we feel we have repeatedly responded clearly to each of these criticism, we propose to agree to disagree.

Ole Jakob Storebø, Psychiatric Research Unit, Psychiatric Department, Region Zealand, Denmark

Morris Zwi, Islington CAMHS, Whittington Health, London, UK

Carlos Renato Moreira-Maia, Federal University of Rio Grande do Sul, Porto Alegre, Brazil

Camilla Groth, Pediatric Department, Herlev University Hospital, Herlev, Denmark

Donna Gillies, Western Sydney Local Health District; Mental Health, Parramatta, Australia

Erik Simonsen, Psychiatric Research Unit, Psychiatric Department, Region Zealand, Denmark

Christian Gluud, Copenhagen Trial Unit, Centre for Clinical Intervention Research, Rigshospitalet, Copenhagen University Hospital, Copenhagen, Denmark

On 2017 Feb 04, Misha Koksharov commented:

It's quite interesting that this type of cyclization doesn't prevent the necessary C-domain rotation and luciferase remains fully active.

Fig. 8 needs some corrections: 1) The pH values are swapped in the figure caption [(A) pH 5.5 and (B) pH 7.8]. 2) Probably, there is some problem with pH adjustment for pH 5.5. P. pyralis luciferase should give nearly monomodal red spectrum at pH 5.5, maybe with a faint green shoulder (Branchini BR, 2007, Oba Y, 2012, Riahi-Madvar A, 2009). Here it is only a faint red shoulder.

On 2016 Oct 22, Lydia Maniatis commented:

As is well-known, perceived color and lightness are contingent on the distribution of luminance/chromaticity in the proximal stimulus and on the corresponding structure of the percept, via the visual process and the principles instantiated therein.

This being the case, any conclusions regarding perceived color contrast that do not explicitly include structure in the discussion will not generalize but will be strictly ad hoc. The results of the present study apply to "plaids", and surely not all plaids, as a category, given the relevance of particular chromaticity values and distributions. The title of the paper, however, implies generality.

The authors also inappropriately leave structure out of the conversation when they speculate that:

"Superimposed luminance and color contrast without co-alignment commonly occurs in natural scenes when shadows or shading fall on a colored surface, whereas co-aligned color and luminance borders are indicative of object and material boundaries, suggesting these two situations activate different color-luminance interactions. "

As descriptions the terms "superimposed luminance and color contrast without co-alignment" and "co-aligned color and luminance borders" are not specific enough, being structure-blind, to assure whether and where "shadows" and "object boundaries" will result in the percept. An easy example, always to hand are the amodally-completed boundaries (which occur in addition to the subjective contours) in the Kanizsa triangle, as well as the appearance of overlap within figures without a luminance step, as well as situations in which the color spectrum or intensity range is shifted and which produce the impression of colored illumination or shading. Whether two areas are interpreted as overlapping ("superimposed" is a description of the percept not the proximal stimulus or the stimulus presented on a screen) depends on relative surface properties and their shapes, not simple "alignments."

So to refer to two different "situations" on the basis of the result - the percept - and to assume different mechanisms ("different color-luminance interactions), without adequately specifying a priori how these two situations are differentiated with respect to the stimulus structure, is putting the cart before the horse.

On 2016 Oct 11, Alem Matthees commented:

References for the above comment

1) Hawkes N. Freedom of information: can researchers still promise control of participants' data? BMJ. 2016 Sep 21;354:i5053. doi: 10.1136/bmj.i5053. PMID: 27654128. http://www.bmj.com/content/354/bmj.i5053

2) White PD, Goldsmith KA, Johnson AL, Potts L, Walwyn R, DeCesare JC, Baber HL, Burgess M, Clark LV, Cox DL, Bavinton J, Angus BJ, Murphy G, Murphy M, O'Dowd H, Wilks D, McCrone P, Chalder T, Sharpe M; PACE trial management group. Comparison of adaptive pacing therapy, cognitive behaviour therapy, graded exercise therapy, and specialist medical care for chronic fatigue syndrome (PACE): a randomised trial. Lancet. 2011 Mar 5;377(9768):823-36. doi: 10.1016/S0140-6736(11)60096-2. Epub 2011 Feb 18. PMID: 21334061. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3065633/

3) Confidentiality: NHS Code of Practice. November 2003. https://www.gov.uk/government/publications/confidentiality-nhs-code-of-practice

4) General Medical Council (2009). Confidentiality guidance: Research and other secondary uses. http://www.gmc-uk.org/guidance/ethical_guidance/confidentiality_40_50_research_and_secondary_issues.asp

5) Queen Mary University of London. PACE trial protocol: Final version 5.2, 09.03.2006. A1.6-A1.7 [Full Trial Consent Forms] https://www.whatdotheyknow.com/request/203455/response/508208/attach/3/Consent forms.pdf

6) Appeal to the First-tier Tribunal (Information Rights), case number EA/2015/0269: http://informationrights.decisions.tribunals.gov.uk/DBFiles/Decision/i1854/Queen Mary University of London EA-2015-0269 (12-8-16).PDF

7) Tracking switched outcomes in clinical trials. http://compare-trials.org/

8) White PD, Chalder T, Sharpe M, Johnson T, Goldsmith K. PACE trial authors' reply to letter by Kindlon. BMJ. 2013 Oct 15;347:f5963. doi: 10.1136/bmj.f5963. PMID: 24129374. http://www.bmj.com/content/347/bmj.f5963

9) Goldsmith KA, White PD, Chalder T, Johnson AL, Sharpe M. The PACE trial: analysis of primary outcomes using composite measures of improvement. Queen Mary University of London. 8 September 2016. http://www.wolfson.qmul.ac.uk/images/pdfs/pace/PACE_published_protocol_based_analysis_final_8th_Sept_2016.pdf

10) Wikipedia. Multiple comparisons problem. Accessed 02 October 2016. https://en.wikipedia.org/wiki/Multiple_comparisons_problem

11) Matthees A, Kindlon T, Maryhew C, Stark P, Levin B. A preliminary analysis of ‘recovery’ from chronic fatigue syndrome in the PACE trial using individual participant data. Virology Blog. 21 September 2016. http://www.virology.ws/wp-content/uploads/2016/09/preliminary-analysis.pdf

12) Tuller D. Trial By Error, Continued: Questions for Dr. White and his PACE Colleagues. Virology Blog. 4 January 2016. http://www.virology.ws/2016/01/04/trial-by-error-continued-questions-for-dr-white-and-his-pace-colleagues/

13) Walwyn R, Potts L, McCrone P, Johnson AL, DeCesare JC, Baber H, Goldsmith K, Sharpe M, Chalder T, White PD. A randomised trial of adaptive pacing therapy, cognitive behaviour therapy, graded exercise, and specialist medical care for chronic fatigue syndrome (PACE): statistical analysis plan. Trials. 2013 Nov 13;14:386. doi: 10.1186/1745-6215-14-386. PMID: 24225069. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4226009/

14) White PD, Goldsmith K, Johnson AL, Chalder T, Sharpe M. Recovery from chronic fatigue syndrome after treatments given in the PACE trial. Psychol Med. 2013 Oct;43(10):2227-35. doi: 10.1017/S0033291713000020. PMID: 23363640. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3776285/

15) Beth Smith ME, Nelson HD, Haney E, et al. Diagnosis and Treatment of Myalgic Encephalomyelitis/Chronic Fatigue Syndrome. Rockville (MD): Agency for Healthcare Research and Quality (US); 2014 Dec. (Evidence Reports/Technology Assessments, No. 219.) July 2016 Addendum. Available from: http://www.ncbi.nlm.nih.gov/books/NBK379582/

16) Matthees A. Treatment of Myalgic Encephalomyelitis/Chronic Fatigue Syndrome. Ann Intern Med. 2015 Dec1;163(11):886-7. doi: 10.7326/L15-5173. PMID: 26618293. http://www.ncbi.nlm.nih.gov/pubmed/26618293

17) Kennedy A. Authors of our own misfortune?: The problems with psychogenic explanations for physical illnesses. CreateSpace Independent Publishing Platform. 4 September 2012. ISBN-13: 978-1479253951. https://www.amazon.com/Authors-our-own-misfortune-explanations/dp/1479253952

18) Sharpe M, Goldsmith KA, Johnson AL, Chalder T, Walker J, White PD. Rehabilitative treatments for chronic fatigue syndrome: long-term follow-up from the PACE trial. Lancet Psychiatry. 2015 Dec;2(12):1067-74. doi: 10.1016/S2215-0366(15)00317-X. Epub 2015 Oct 28. PMID: 26521770. https://www.ncbi.nlm.nih.gov/pubmed/26521770

19) Higgins PTJ, Altman DG, Sterne JAC; on behalf of the Cochrane Statistical Methods Group and the Cochrane Bias Methods Group. Chapter 8: Assessing risk of bias in included studies. Version 5.1.0 [updated March 2011]. http://handbook.cochrane.org/chapter_8/8_assessing_risk_of_bias_in_included_studies.htm

20) Schulz KF, Grimes DA. Blinding in randomised trials: hiding who got what. Lancet. 2002 Feb 23;359(9307):696-700. PMID: 11879884. http://www.who.int/rhl/LANCET_696-700.pdf

21) Boot WR, Simons DJ, Stothart C, Stutts C. The Pervasive Problem With Placebos in Psychology: Why Active Control Groups Are Not Sufficient to Rule Out Placebo Effects. Perspect Psychol Sci. 2013 Jul;8(4):445-54. Doi: 10.1177/1745691613491271. PMID: 26173122. http://pps.sagepub.com/content/8/4/445.long

22) Button KS, Munafò MR. Addressing risk of bias in trials of cognitive behavioral therapy. Shanghai Arch Psychiatry. 2015 Jun 25;27(3):144-8. doi: 10.11919/j.issn.1002-0829.215042. PMID: 26300596. http://www.ncbi.nlm.nih.gov/pmc/articles/PMC4526826

23) Wood L, Egger M, Gluud LL, Schulz KF, Jüni P, Altman DG, Gluud C, Martin RM, Wood AJ, Sterne JA. Empirical evidence of bias in treatment effect estimates in controlled trials with different interventions and outcomes: meta-epidemiological study. BMJ 336 (7644): 601–5. DOI:10.1136/bmj.39465.451748.AD. PMID 18316340. PMC 2267990. http://www.bmj.com/cgi/content/full/336/7644/601

24) Kindlon TP. Objective measures found a lack of improvement for CBT & GET in the PACE Trial: subjective improvements may simply represent response biases or placebo effects in this non-blinded trial. BMJ Rapid Response. 18 January 2015. http://www.bmj.com/content/350/bmj.h227/rr-10

25) Knoop H, Wiborg J. What makes a difference in chronic fatigue syndrome? Lancet Psychiatry. 2015 Feb;2(2):113-4. doi: 10.1016/S2215-0366(14)00145-X. Epub 2015 Jan 28. PMID: 26359736. https://www.ncbi.nlm.nih.gov/pubmed/26359736

26) johnthejack (Peters J). Using public money to keep publicly funded data from the public. 29 June 2016. https://johnthejack.com/2016/06/29/using-public-money-to-keep-publicly-funded-data-from-the-public/

27) Coyne JC. Further insights into war against data sharing: Science Media Centre’s letter writing campaign to UK Parliament. 31 January 2016. https://jcoynester.wordpress.com/2016/01/31/further-insights-into-the-war-against-data-sharing-the-science-media-centres-letter-writing-campaign-to-uk-parliament/

On 2016 Oct 11, Alem Matthees commented:

On 4 October 2016 I submitted a BMJ Rapid Response to this article but one week later it has not been posted on the BMJ website ( http://www.bmj.com/content/354/bmj.i5053/rapid-responses ). I am not sure whether this delay is normal or if it has been rejected. So I will post it on PubMed Commons. The following is as previously submitted, except for the addition of one word to help clarify a sentence, and the addition of a PMID for reference 22 (and removing a stray character). I also had to move the references to a separate PubMed Commons comment below this one:

The PACE trial investigators never had total control over the data to begin with

Thank you for covering this issue. Some comments:

a) This article states that it was “not possible” to contact me[1]. However, my email address shows up in the first page of results with a Google search for Alem Matthees.

b) Regarding the modification of consent forms for future trials to address FOIA data releases. The FOIA was implemented in January 2005, before PACE trial participants were recruited[2]; under the legislation, trial data that is unlikely to identify participants is not personal data, and it was always QMUL’s responsibility to be aware that trial data is within scope of the FOIA, but they failed to inform participants of this possibility. Similarly, confidentiality guidelines from the NHS[3] and GMC[4] state that consent is not necessary to release de-identified data. The trial consent form promised that identities will be protected[5], and they have been. The Information Commissioner and Information Tribunal considered and rejected the assertions that FOIA data releases would significantly affect recruitment in future studies[6].

c) The lesson here is not about ‘controlling’ data, it is that if data is not analysed or published in a fair and transparent way, people will seek to acquire and re-analyse it, particularly when debatable claims were made that affect the lives of millions of patients. The major deviations from the published trial protocol, the recovery criteria in particular, is what motivated me. Outcome switching is recognised as a major problem in the research community[7].

While it was important to find out the protocol-specified primary outcomes that were abandoned, the changes to the recovery criteria (a secondary analysis) were the most problematic. I sought the data after QMUL refused to release the protocol-specified outcomes for improvement and recovery. It is misleading to promote ‘recovery’ rates of 22% when based on indefensible criteria, such as thresholds of ‘normal’ fatigue and physical function that overlap with trial eligibility criteria for severe disabling fatigue, and where one-third still met Oxford CFS criteria.

d) White et al. previously downplayed the changes to the primary outcomes as the primary measures “were the same as those described in the protocol”[8]. Now that the results for the protocol-specified primary outcomes are known and people are comparing them with the post-hoc equivalents, Professor White is arguing that “They’re not comparing like with like […] They are comparing one measure with a completely different one—it’s apples and pears”.[1]

Professor White also stated that going back to the protocol makes no difference, as adjunctive CBT and GET are still statistically significantly better than specialist medical care alone[1]. However, statistical significance is not the same as clinical significance, and going back to the protocol decreases the response rates in the CBT and GET groups from approximately 60% down to 20% (compared to 45% down to 10% for SMC alone)[9].

While it may be argued that the above does not change the conclusion that adjunctive CBT and GET are superior to SMC alone, the trial investigators conducted many analyses without correcting for multiple comparisons[10]; based on a quick look at the p values, some of the differences reported may not be statistically significant when using a more conservative approach.

Moreover, the data has been re-analysed and going back to the protocol not only decreased the 'recovery' rates from 7-22% down to to 2-7%, but the differences between adjunctive therapy groups and SMC alone are not significant[11]. There appears to be a consistent pattern of outcome switching and major changes to thresholds that inflate the results by several times over.

e) The article states that White et al. “had answered critics who have made legitimate scientific points”. However, there are numerous legitimate questions or problems that are unaddressed[12].

f) The article states that out of 37 FOIA requests made, “many” were rejected as vexatious. But only 3 or so have been rejected under S.14 (e.g. see whatdotheyknow.com), the first one was in relation to details about the timing and nature of the changes to the protocol, the other two or so by others, relating to trial data. Asking for trial data or for details about methodology is not harassment.

g) It remains unclear whether all the changes to the trial protocol were made and independently approved before analysing data. Statements about this issue appear to relate to the 2011 Lancet paper only, but there is no mention of change to the recovery criteria in the statistical analysis plan that was finalised shortly before the unmasking of data[13]. The ‘normal range’ is described in the 2011 Lancet paper as a post-hoc analysis[2], and this ‘normal range’ then formed part of the revised recovery criteria published in Psychological Medicine in 2013[14] without any mention of approval. I urge the trial investigators to clarify once and for all whether the changes to the recovery criteria were made after the unmasking of any trial data and whether these were independently approved.

h) Patients want to get better but many are simply not impressed with the methodology or results of PACE: 80% of candidates definitely or provisionally diagnosed with CFS were excluded from the trial[2]. The CFS and ME case criteria used were problematic[15-17]. Only a small minority of broadly defined CFS patients reported benefit from CBT or GET (around 10-15% over SMC). That benefit was modest and transient, with no significant advantages at 2.5 year follow-up[18].

Subjective self-reports are important, but modest improvements are difficult to separate from a placebo response and other reporting biases when a trial is non-blinded and tests therapies that aim to change patients’ perceptions about their illness[19-23]. This issue becomes more relevant given that there was a complete absence of meaningful improvements to multiple objective outcomes[24] (the small improvement in walking distance for the GET group has been attributed by CBT/GET proponents to participants pushing themselves harder on the test rather than being fitter[25]).

i) QMUL spent £245,745 on legal fees trying to prevent release of the requested data[26], and were also part of a failed lobbying attempt to be removed from the FOIA[27].

References

[continued below...]

On 2016 Sep 26, Peter Hajek commented:

The title asserts that smokers who switch to vaping start to drink more. The paper however shows no such thing. It just reports that ex-smokers who vape drink more than ex-smokers who do not vape. Heavier smokers are more likely to seek nicotine maintenance and are also heavier drinkers and the difference almost certainly predated quitting. The title does not reflect the study findings and misleads casual readers.

On 2016 Sep 30, Wasim Maziak commented:

None

On 2016 Sep 26, Peter Hajek commented:

The letter has a misleading title, it identifies no 'unsubstantiated claims'. It just says that some ex-smokers would quit anyway and that surveys have a margin of error. It raises no material issues that would suggest that the article's finding of a huge number of smokers who claim to have stopped smoking with the help of e-cigarettes is inaccurate.

On 2016 Oct 27, James Yeh commented:

Editor's Comment Obesity and Management of Weight Loss — Polling Results

James Yeh, M.D., M.P.H., and Edward W. Campion, M.D.

Obesity is increasingly prevalent worldwide, and about 40% of Americans meet the diagnostic criteria for obesity.[1] The goal of weight loss is to reduce the mortality and morbidity risks associated with obesity. Patients with a body-mass index (BMI) in the range that defines obesity (>30) have a risk of death that is more than twice that of persons with a normal BMI.[2] Obesity is also associated with increased risks of cardiovascular disease, diabetes, and several cancers. A recent study suggests that being overweight or obese during adolescence is strongly associated with increased cardiovascular mortality in adulthood.[3] Studies suggest that even a 5% weight loss may reduce the complications associated with obesity.[4]

In September 2016, we presented the case of Ms. Chatham, a 29-year-old woman with class I obesity (BMI, 32) who leads a fairly sedentary lifestyle, with frequent reliance on takeout foods and with infrequent physical activity.[5] Readers were invited to vote on whether to recommend initiating treatment with one of the FDA-approved drugs for weight loss along with lifestyle modifications or to recommend only nonpharmacologic therapies and maximizing lifestyle changes. The patient has no coexisting medical conditions, but her blood pressure is slightly elevated (144/81 mm Hg). In the past, Ms. Chatham has tried to lose weight using various diets, each time losing 10 to 15 lb (4.5 to 6.8 kg), but she has never been able to successfully maintain weight loss.

Over 85,000 readers viewed the Clinical Decisions vignette during the polling period, and 905 readers from 91 countries voted in the informal poll. The largest group of respondents (366) was from the United States or Canada, representing nearly 40% of the votes. A large majority of the readers (80%) voted against prescribing one of the FDA-approved medications for weight loss and instead recommended maximizing lifestyle modification and nonpharmacologic therapies first.

A substantial proportion of the 64 Journal readers who submitted comments expressed concern about the absence of efficacy data on long-term follow-up and about the side effects associated with current FDA-approved medications for weight loss. Some suggested that simply treating obesity with a prescription medication is shortsighted and that it is important to uncover patients’ motivations for existing lifestyle choices and for weight loss. The commenters emphasized the need for a multifaceted approach to obesity management that includes nutritional and psychological support, as well as stress management, with the goal of long-lasting improvement in exercise and eating habits that will lead to weight reduction and maintenance of a healthier weight.

Some commenters, noting the difficulty of lifestyle changes, felt that pharmacotherapy can be a complementary and reasonable part of a multidisciplinary treatment plan. Some wrote that obesity should be managed as a chronic disease is managed and that an inability to lose weight should not be seen as a disciplinary issue, especially given the importance of genetic and physiological factors. These commenters argued that the use of pharmacotherapy as part of the treatment plan to achieve weight loss should not be stigmatized.

Overall, the results of this informal Clinical Decisions poll indicate that a majority of the respondents think physicians should not initially recommend the use of an FDA-approved drug as part of a weight-loss strategy, at least not for a patient such as Ms. Chatham, and that many respondents were troubled by the current uncertainties about the long-term efficacy and safety of weight-loss drugs.

REFERENCES 1. Flegal KM, Kruzon-Moran D, Carroll MD, Fryar CD, Ogden CL. Trends in obesity among adults in the United States, 2005 to 2014. JAMA 2016;315:2284-91. 2. Global BMI Mortality Collaboration. Body-mass index and all-cause mortality: individual-participant-data meta-analysis of 239 prospective studies in four continents. Lancet 2016;388:776-86. 3. Twig G, Yaniv G, Levine H, et al. Body-mass index in 2.3 million adolescents and cardiovascular death in adulthood. N Engl J Med 2016;374:2430-40. 4. Kushner RF, Ryan DH. Assessment and lifestyle management of patients with obesity: clinical recommendations from systematic reviews. JAMA 2014;312:943-52. 5. Yeh JS, Kushner RF, Schiff GD. Obesity and management of weight loss. N Engl J Med 2016;375;1187-9.

On 2016 Oct 11, Richard Kellermayer commented:

Great work!

It would have been nice, however, to see our work on the mucosal mycobiome in pediatric Crohn disease patients discussed and referenced:

Microbiota separation and C-reactive protein elevation in treatment-naïve pediatric granulomatous Crohn disease. Kellermayer R, Mir SA, Nagy-Szakal D, Cox SB, Dowd SE, Kaplan JL, Sun Y, Reddy S, Bronsky J, Winter HS. J Pediatr Gastroenterol Nutr. 2012 Sep;55(3):243-50. doi: 10.1097/MPG.0b013e3182617c16. PMID: 22699834

On 2016 Oct 03, Atanas G. Atanasov commented:

"Many "rules" for writing good science abstracts associate with fewer citations":

https://twitter.com/mattjhodgkinson/status/594865422840762368 ...and... http://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1004205

...another study pointing in the same direction as our work.

On 2016 Sep 21, Murat Büyükşekerci commented:

In my opinion there is problem with title of this article. Since the term "mediator" refers to intracellular proteins that enhance and activate the functions of other proteins. Thiol/disulphide homeostasis is a term used to describe the redox state of mileu and could not be defined as a novel mediator. Thanks for regarding.

On 2016 Oct 16, Thomas Langer commented:

Loss of m-AAA proteases increases mitochondrial Ca2+ influx at low cytosolic [Ca2+]

We demonstrate in our paper that the m-AAA protease (AFG3L2/SPG7) degrades EMRE, an essential subunit of the mitochondrial Ca2+ uniporter MCU. Loss or decrease of m-AAA protease activity, as observed in SCA28, impairs the assembly of MCU with the gatekeeper subunits MICU1/2 and results in the formation of unregulated, open MCU. This causes an increased mitochondrial Ca2+ influx at low cytosolic [Ca2+] and renders neurons more susceptible to Ca2+ overload, opening of the mitochondrial permeability transition pore (MPTP) and cell death. Thus, we do not propose in our manuscript that the formation of deregulated MCU causes an increase in cytosolic [Ca2+], as suggested in the comment by Casari et al.. Our findings explain the striking observation by the Casari group that reduced Ca2+ influx into AFG3L2-deficient neurons (by pharmacological inhibition or genetic ablation of mGluR1) protects against neuronal death (Maltecca et al., 2015): lowered cytosolic [Ca2+] in these settings result in decreased mitochondrial Ca2+ influx via deregulated MCU lacking gatekeeper subunits in AFG3L2-deficient neurons, thus preventing mitochondrial Ca2+ overload. Of note, our findings are also in agreement with two recent studies in MICU1-deficient mice demonstrating that deregulated Ca2+ influx causes MPTP opening-induced cell death (Antony et al., Nat. Com., 2016) and ataxia by specifically affecting Purkinje cells (Liu et al., Cell Reports, 2016). Strikingly, reduced EMRE expression was found to suppress ataxia (Liu et al., Cell Reports, 2016).

Casari et al. have suggested that other (yet poorly understood) functions of the m-AAA protease lower the mitochondrial membrane potential (Maltecca et al., 2015) and impair mitochondrial morphology (Maltecca et al., 2012), resulting in decreased mitochondrial Ca2+ influx. Our results do not support a major role of disturbed mitochondrial morphology (Fig. 7), but we agree (and confirm in Fig. S6) that lowering the mitochondrial membrane potential decreases mitochondrial Ca2+ influx after histamine stimulation. We therefore have assessed mitochondrial Ca2+ influx upon mild increase of cytosolic [Ca2+] and observed an increased Ca2+ influx into m-AAA protease-deficient mitochondria (Fig. 6). The rationale of this protocol relies on the sigmoidal relationship between mitochondrial Ca2+ influx and extramitochondrial [Ca2+]. In resting conditions, mitochondrial Ca2+ accumulation is negligible when cytosolic [Ca2+] is below a threshold (~500 nM). Inhibition of SERCA leads to ER Ca2+ leaks, thus causing a slow and small increase of cytosolic [Ca2+]. In this experimental setup (low cytoplasmic [Ca2+]), mitochondrial Ca2+ influx is less hampered by a reduced mitochondrial membrane potential and indeed we observed an increased mitochondrial Ca2+ influx in AFG3L2-deficient mitochondria. We therefore suggest (and discuss in our manuscript) that m-AAA protease-deficient mitochondria show increased Ca2+ influx at resting [Ca2+] but decreased Ca2+ influx at high Ca2+ concentrations (due to the lowered membrane potential).

Casari et al. also raise doubts about the relative role of Ca2+ and mtROS for MPTP opening. We demonstrate a reduced Ca2+ retention capacity of AFG3L2-deficient mitochondria in vitro and in vivo, which correlates with the increased mitochondrial Ca2+ influx (observed upon SERCA inhibition) and the increased ROS levels in AFG3L2-deficient mitochondria. Increased mitochondrial Ca2+ influx under resting conditions is known to trigger MPTP opening (Antony et al., Nat. Com., 2016) and to cause increased mtROS production (Hoffman et al., Cell Reports, 2013; Mallilankaraman et al., Cell, 2012). Thus, both events are interdependent and their relative contribution to MPTP opening is difficult to dissect. We have not addressed this issue in the present manuscript and, by no means, exclude a contribution of mtROS to MPTP opening.

Together, our results provide compelling evidence that m-AAA protease deficiency causes the accumulation of MCU-EMRE complexes lacking gatekeeper subunits and impairs mitochondrial Ca2+ handling, sensitizing neurons for MPTP opening. The relative contribution of deregulated mitochondrial Ca2+ influx and lowered mitochondrial membrane potential for disease pathogenesis is currently difficult to assess and certainly warrants further studies in appropriate mouse models. However, we would like to point out that other mitochondrial diseases affecting respiration and the formation of the mitochondrial membrane potential do not show the striking vulnerability of Purkinje cells seen in SCA28. At the same time, MCU-dependent mitochondrial Ca2+ influx is a crucial determinant of excitotoxicity in neurons (Qui et al., Nat. Com., 2013). This study also demonstrates that synaptic activity transcriptionally suppresses MCU expression thereby counteracting mitochondrial Ca2+ overload at high cytosolic [Ca2+] and preventing induction of excitotoxicity. Our results thus open up the attractive possibility that increased Ca2+ influx under resting conditions and the accompanying mild stress increases progressively the vulnerability of Purkinje cells, causing late-onset neurodegeneration in SCA28 patients, which are only heterozygous for mutations in AFG3L2.

On 2016 Oct 13, Giorgio Casari commented:

Increased or decreased calcium influx?

In this elegant paper the authors propose that loss of m-AAA (i.e. the depletion of both SPG7 and AFG3L2) facilitates the formation of active MCU complexes through the increased availability of EMRE, thus (i) increasing calcium influx into mitochondria, (ii) triggering MPTP opening and (iii) causing the consequent increase of neuronal cytoplasmic calcium leading to neurodegeneration. We previously reported that loss or reduction of AFG3L2 causes (i) decreased mitochondrial potential and fission, thus (ii) decreased calcium entry and (iii) the consequent augmented neuronal cytoplasmic calcium leading to neurodegeneration. While the functional link of m-AAA with MAIP and MCU-EMRE represents a new milestone in the characterization of the roles this multifaceted protease complex, we would like to comment on the conclusions pertaining to the calcium dynamics. 1. In SPG7/AFG3L2 knock-down HeLa cells (Figure S6A) mitochondrial matrix calcium is dramatically reduced (approx. from 100 to 50 microM) following histamine stimulation, which triggers IP3-mediated calcium release from ER. This reduction is in complete agreement with the one we previously detected in Afg3l2 ko MEFs (Maltecca et al., 2012), and that we also confirmed in Afg3l2 knock-out primary Purkinje neurons (the cells that are primarily affected in SCA28) upon challenge with KCl (Maltecca et al., 2015). The decreased mitochondrial calcium uptake correlates with the 40% reduction of mitochondrial membrane potential in SPG7/AFG3L2 knock-down cells (Figure S6B), as expected since the mitochondrial potential is the major component of the driving force for calcium uptake by MCU. Accordingly, these data are in line with the decreased mitochondrial membrane potential observed in Afg3l2 knock-out Purkinje neurons (Maltecca et al., 2015). We think that this aspect is central, because the respiratory defect is the primary event associated to m-AAA deficiency and neurodegeneration. So, the data of König et al. agree with our own findings that mitochondrial matrix calcium is reduced after m-AAA depletion. 2. By a different protocol (SERCA pumps inhibition and ER calcium leakage; Figure 6 C-F), the authors detected a small increase of mitochondrial calcium concentration in SPG7/AFG3L2 knock-down HeLa cells (from approx. 3 to 6 microM). The huge difference in calcium concentration detected in the two experiments (100 to 50 microM in Figure S6A and 3 to 6 microM in Figure 6 C) possibly reflects the stimulated (histamine) vs. unstimulated (calcium leakage) conditions, this latter being more difficult to correlate to physiologic neuronal situation. 3. The authors show increased sensitivity to MPTP opening in the absence of m-AAA and they propose the consequent calcium release as the cause of calcium deregulation and neuronal cell death. ROS are strong sensitizers of MPTP to calcium and thus favor its opening. It is well known that m-AAA loss massively increases intramitochondrial ROS production. Thus, higher ROS levels, rather than high calcium concentrations, can be the trigger of MPTP opening. Taking all this into consideration, we think that mitochondrial depolarization (as shown in Figure S6B) and decreased mitochondrial calcium entry (Fig S6A), even in the presence of increased amount of MCU-EMRE complexes, may lead to inefficient mitochondrial calcium buffering and, finally, to cytoplasmic calcium deregulation. ROS dependent MPTP opening, which may occur irrespective of a low matrix calcium concentration, may additionally contribute to this final event.

Minor comment At page 7 we read: “Notably, these experiments likely underestimate the effect on mitochondrial Ca2+ influx observed upon loss of the m-AAA protease, since the loss of the m-AAA protease also decreases ΔΨ (i.e., the main force driving mitochondrial Ca2+ influx), as revealed by the significant impairment of mitochondrial Ca2+ influx triggered by histamine stimulation (Maltecca et al., 2015) (Figures S6A–S6E)”. The reference is not appropriate, since in Maltecca et al., 2015 the reduced mitochondrial calcium uptake has been demonstrated in Afg3l2 knock-out Purkinje neurons upon challenge with KCl and not with histamine. We used histamine stimulation, which triggers IP3-mediated calcium release from ER, in Afg3l2 ko MEF in a previous publication (Maltecca F, De Stefani D, Cassina L, Consolato F, Wasilewski M, Scorrano L, Rizzuto R, Casari G. Respiratory dysfunction by AFG3L2 deficiency causes decreased mitochondrial calcium uptake via organellar network fragmentation. Hum Mol Genet. 2012, 21:3858-70. doi: 10.1093/hmg/dds214).

On 2016 Nov 30, Gwinyai Masukume commented:

According to this 2016 Maternal Health Lancet Series paper, unlike for most African countries no data was available for the number of obstetricians and gynaecologists and midwives in South Africa precluding the calculation of the ratio of these practitioners per 1000 pregnancies. This deficit of South African data also applies to the Caesarean section rate global estimates from the World Health Organization published this year in another journal Betrán AP, 2016.

The apparent lack of data from South Africa suggests that it has ‘fallen off’ the international maternal health map. However, the Health Professions Council of South Africa Holmer H, 2015 and the South African Nursing Council have contemporary and historical data on the number of obstetricians and gynaecologists and midwives respectively. Caesarean delivery rates are available from the Health Systems Trust.

Because information from The Lancet and the World Health Organization has a global reach and influences key policy makers, this high level lack of visibility of pertinent South African maternal health data is concerning. Maternal health metrics are “essential to guide intervention research, set implementation priorities, and improve quality of care, particularly for women and babies most at risk” Koblinsky M, 2016.

Efforts to quickly address this lack of visibility are warranted.

On 2017 Feb 06, GARRET STUBER commented:

*This review was completed as part of a graduate level circuits and behavior course at UNC-Chapel Hill. The critique was written by students in the class and edited by the instructor, Garret Stuber.

Comments and critique

Written by Li et al., this paper investigated a class of oxytocin receptor interneurons (OxtrINs) on which the same group first characterized in 2014 [1]. OxtrINs are a subset of somatostatin positive interneurons in the medial prefrontal cortex (mPFC) that seem to be important for sociosexual behaviors in females, specifically during estrus and not diestrus. To complement their previous story, here the authors concluded that OxtrINs in males regulate anxiety-related behaviors through the release of corticotropin releasing hormone binding protein (Crhbp). While we agree that these neurons could be mediating sexually dimorphic behaviors, it is unclear how robust these differences really are.

We had some technical issues with this paper. First, it is unclear exactly how many mice were allotted to each experimental group, and it would have been useful to see individual data in each of the behavioral experiments, so that we can better understand some of the variability in the authors’ graphs. Even among different experiments, there were variable sizes of n (e.g. Fig. 5F-H, “n = 8-14 mice per group”). There was also no mention of how many cells per animal were tested for each brain slice experiment; instead, we received total numbers of cells tested per group. This paper did not include the complementary female data to Fig. 4F-G and Fig. 5A-B, the experiments pairing blue light with Crhr1 antagonist or Crhbp antagonist. We would have appreciated seeing this data adjacent to that for the males. In addition, there was no mentioned control for the optogenetic experiments. The authors only compared responses between light on and light off trials. Typically in optogenetic approaches, a set of control mice are also implanted with optic fibers and flashed with blue light in the absence of virus to test whether the light alone influences behavior. Incidentally, there is evidence that blue light influences blood flow, which may affect neuronal activity [2]. It was also unclear during the sociosexual behavioral testing whether the males were exposed to females in estrus or diestrus. In all, lack of detailed sample sizes and controls made it difficult to assess how prominent these sex differences were.

These issues aside, knocking out endogenous Oxtr in their targeted interneuron population was a key experiment, as it demonstrated that oxytocin signaling in OxtrINs is important in anxiety-related behaviors in males, but not in females regardless of the estrus stage. They did this using a floxed Oxtr mouse and deleted OxtR using a Cre-inducible virus, allowing for temporal and cell-type-specific control of this deletion, and subsequently measured the resulting phenotype using an elevated plus maze and open field task. The authors also validated that changes in exploration were not due to hyperactivity. We think these experiments are convincing.

TRAP profiling, which the same research group pioneered in 2014 [3], provided a set of genes enriched in OxtrINs. TRAP targets RNAs while they are translated into proteins, so we think their results here are particularly relevant. Moreover, the authors provided a list of genes enriched in sex-specific OxtrINs, a useful resource for those interested in gene expression differences in males and females. Once they identified Crhbp, an inhibitor of Crh, they hypothesized that OxtrINs were releasing Crhbp to modulate anxiogenic behaviors in males. The authors next measured Crh levels in the paraventricular nucleus of the hypothalamus and found that Crh levels are higher in females than males. They thus concluded Crh levels were driving sex differences associated with OxtrINs. We wonder whether Crh levels are also higher in the female mPFC, but we agree here too.

To demonstrate that Crhbp expressed by OxtrINs is important in modulating anxiety-like behaviors in males, the authors targeted Crhbp mRNA using Cre-inducible viral delivery of an shRNA construct and subsequently tested anxiety-related behaviors. They found that knocking down Crhbp was anxiogenic in males and not in females. This was a critical experiment, but the shRNA constructs targeting Crhbp were validated solely in a cell line. It would have been more appropriate to perform a western blot on mPFC punches of adult mice, showing whether this lentiviral construct knocked down Crhbp expression in the mouse brain prior to behavioral testing. In fact, it also would have been useful to see a quantification of the shRNA transfection rate, as well as its specificity in vivo. As stated above, we also do not know the distribution of behavioral responses here either. Without these pieces of information, it is difficult to assess how reliable or robust their knockdown was.

The authors concluded that sexually dimorphic hormones act through the otherwise sexually monomorphic OxtrINs to regulate anxiety-related behaviors in males and sociosexual behaviors in females. We agree that OxtrINs interact with oxytocin and Crh to bring about sex-specific phenotypes, but we also think that using additional paradigms testing anxiety and social behaviors, such as a predator odor, novelty-suppressed feeding or social grooming, could shed more light on the nuances of mPFC circuitry. In addition, the authors suggested that OxtrINs are sexually monomorphic because they are equally abundant in males and females. The authors’ TRAP data however suggested that OxtrINs of males and females have different gene expression profiles (Table S2), thus indicating that these interneurons may form different connections in each sex that mediate the electrophysiological and behavioral differences we see in this study.

It would be interesting to overexpress Crhbp in female mice, preferably in a cell-type-specific manner, to see whether female mice would demonstrate the anxiety-like behavior seen in males. If the Crh:Crhbp balance is in fact mediating this sexually dimorphic behavior through OxtrINs, we would expect that doing these manipulations may “masculinize” the females’ behavior. Regardless, we believe that this study opens opportunities for future work into how oxytocin and Crh release from the hypothalamus may act together to coordinate behavior. It will also be interesting to see if single-cell RNA sequencing could provide insight into whether OxtrINs can be further divided into sexually dimorphic subtypes. As the authors pointed out, understanding the dynamics of Crh and oxytocin in the mPFC will be important for gender-specific therapy and treatment.

[1] Nakajima, M. et al. Oxytocin modulates female sociosexual behavior through a specific class of prefrontal cortical interneurons. Cell. 159, 295-305 (2014).

[2] Rungta, R. L. et al. Light controls cerebral blood flow in naïve animals. Nature Communications. 8, 14191 (2017).

[3] Heiman, M. et al. Cell-type-specific mRNA purification by translating ribosome affinity purification (TRAP). Nature Protocols. 9, 1282-1291 (2014).

On 2017 Aug 08, Christopher Tench commented:

Could you possibly provide the coordinates analysed otherwise it is difficult to interpret the results.

On 2016 Oct 21, Lydia Maniatis commented:

According to Kingdom: "A longstanding issue in vision research concerns whether the internal noise involved in contrast transduction is fixed or variable in relation to contrast magnitude."

This statement is precisely analogous to saying: A longstanding problem in chemistry is whether phlogiston is evenly or unevenly distributed in relation to object density.

The notion of "internal noise" is crude, lumping together every element of the visual process between light hitting the retina and the conscious percept. It is flatly inconsistent with perceptual experience, which is in no way "noisy," yet most proponents of this view would have us accept that the conscious percept directly reflects "low-level" and noisy spiking activity of individual or sets of neurons. In any event, no attempt has ever been made to corroborate the noise assumption.

It is not even clear what the criteria would be for corroboration on the basis of measurements at the physiological level. It would have to be shown, presumably, that identical "sensory inputs" produce a range and distribution of neural responses, this range and distribution being somewhat predictable; however "inputs" to brain activity don't come only from the external receptor organs, no matter how well we might be able to control these. Even if we could (inconceivably) control inputs perfectly, and even if we were able to say that (as is often claimed) at V1 neural responses are noisy, we would have to explain why this noise doesn't affect the conscious percept (which, again, is very stable) and yet is detectable on the basis of conscious experience. Graham (1992; 2011) has adopted the hypothesis that under certain conditions the brain becomes "transparent" so that the activities at lower levels of the processing hierarchy are act directly on the percept. It should be reasonably clear that such a view isn't worth entertaining, but if one wants to entertain it there are massive theoretical difficulties to overcome. It seems to imply that feedback and feedforward processes for some reason are frozen and some alternative, direct pathway to consciousness exists, all while other pathways are still active (because the inference generally applies to a discontinuity on a screen in a room, all of which are maintained in perception.)

Not surprisingly given the concept's vagueness, the case for "internal noise" has never been credibly made. But it is widely accepted.

Those who simply accept the internal noise assumption "measure internal noise" by analyzing simple "detection and discrimination" datasets on the basis of multiple layers of untested, untestable, or empirically untenable assumptions rolled into "computational models" including indispensable, multiple free parameters. (For a detailed examination of this technique, see PubPeer comments on Pelli (1985)).

In the absence of clear and explicit assumptions, relevant confounds remain unspecified, and tests, as here, are always ad hoc, hinging on particular datasets, and counting up "successes" as though by adding these together, they can outweigh unexplained failures. But failures are dispositive, of course, when we are aiming at a general explanation.

On 2017 Aug 20, Daniel Weiss commented:

The central problem with current standards of Lyme disease diagnosis and treatment is the absence of a highly sensitive and specific test, a gold standard, that can prove the presence of disease and/or demonstrate cure. When a patient complains of unremitting neurological and/or musculo-skeletal symptoms after completing a treatment, persistent infection is the most logical interpretation. Recent microbiological research has uncovered persistence mechanisms in virtually every prokaryotic organism(Conlon, Rowe, & Lewis, 2015 Advances in experimental medicine and biology; Harms, Maisonneuve, & Gerdes, 2016 Science,; Lewis & Shan, 2016 Molecular cell). It is not surprising that a bacterial species adapted to survive in multiple vertebrate hosts, and through multiple stages of the three-year cycle of its invertebrate host, might persist after antibiotic treatment(Feng, Shi, Zhang, & Zhang, 2015 Emerging microbes & infections). Borrelia species are characterized by immense plasticity in their expression of morphology, antigens, and genes.

In the laboratory, and in infected humans, antibiotics predictably induce the persister phenotype(Bijaya Sharma, Autumn V Brown, Nicole E Matluck, Linden T Hu, & Kim Lewis, 2015 Emerging microbes & infections).

Exposed to antibiotics, Borrelia burgdorferi rapidly loses the morphology of “active” motile, dividing spirochetes(Sapi et al., 2016 Int J Med Sci; Timmaraju et al., 2015 FEMS Microbiol Lett). The organism settles into dormancy in biofilm or as round bodies(Merilainen, Herranen, Schwarzbach, & Gilbert, 2015). Yet, it retains antigenicity and the genetic capacity to return to the spirochete form(Merilainen, Brander, Herranen, Schwarzbach, & Gilbert, 2016 Microbiology).

The failure to respond to a particular antibiotic regimen does not equate with "there is no infection present". The more appropriate conclusion may be that the antibiotic is ineffective for this infection. It is completely unclear whether these patients with presumed autoimmune disorders have persistent infection with B. burgdorferi.

On 2017 May 21, Misha Koksharov commented:

To clarify which of the thermostable luciferase mutants was used here (I've made a lot of them in L. mingrelica & P. pyralis Flucs - some are published, some are not):

LMLucR = the mutant G216N,A217L,S398M in Luciola mingrelica firefly luciferase (Koksharov MI, 2011).

On 2017 Feb 09, K Hollevoet commented:

Intramuscular antibody gene transfer as a means for prolonged in vivo antibody expression continues to gain traction as an alternative to conventional antibody production and delivery. The study by Kim et al. presents yet another elegant example of said approach, specifically expressing the anti-HER2 4D5 monoclonal antibody (mAb) in mice via plasmid-based gene electrotransfer. The authors report an average 4D5 peak concentration of up to 152 μg ml−1 in BALB/c mice, two weeks after intramuscular electrotransfer of the 4D5-encoding plasmid DNA (pDNA). mAb levels remained above 120 μg ml−1 for at least a month, as depicted in Figure 3d of the manuscript.¹ These results raise some questions, which, in our opinion, are not sufficiently addressed in the manuscript discussion.

Firstly, plasmid-based antibody gene electrotransfer in mice typically results in mere single-digit μg ml−1 mAb serum levels.² After careful consideration, we found no novelties in pDNA design, optimization or delivery in Kim et al.¹ that could explain their quantum leap in attained mAb titers – up to two log higher than the current available literature.

Secondly, the presented data by Kim et al.¹ surpass the expression levels of viral-based anti-HER2 antibody gene transfer studies in mice, with reported peak 4D5 and trastuzumab concentrations of 30 to 40 μg ml–1.^3,4 This further adds to the surprise, given viral vectors consistently outperform plasmid electrotransfer in terms of transgene expression.²

Thirdly, Figure 4f shows an average 4D5 serum concentration of 3.8 μg ml–1 in athymic nude mice, 22 days after tumor cell injection and, so we assume, approximately two weeks after pDNA delivery.¹ mAb titers in these tumor-bearing mice are thus about 40-fold lower than those in the BALB/c mice. Given identical dosing and delivery conditions were applied, the reason for this discrepancy is unclear. The difference in mAb titers appears too high to e.g. attribute it to inter-experiment or mice strain variability. Target-mediated drug disposition in the tumor-bearing mice, i.e. the binding of 4D5 to HER2, is also unlikely to have such impact, given the continuous and robust in vivo mAb production the authors found.

In conclusion, prolonged in vivo mAb expression above 100 μg ml–1 is unprecedented in non-viral antibody gene transfer. The impact of these findings, however, is mortgaged by the lack of explanation Kim et al. provide on the obvious differences with the available literature and with their own subsequent results – as outlined earlier. To allow for these remarkable findings to advance the field, we respectfully invite the authors to address the above concerns, and provide additional support for their data.

References: 1. Kim H, Danishmalik SN, Hwang H, Sin JI, Oh J, Cho Y, et al. Gene therapy using plasmid DNA-encoded anti-HER2 antibody for cancers that overexpress HER2. Cancer Gene Ther 2016 doi: 10.1038/cgt.2016.37. 2. Suscovich TJ, Alter G. In situ production of therapeutic monoclonal antibodies. Expert Rev Vaccines 2015; 14: 205-19. 3. Jiang M, Shi W, Zhang Q, Wang X, Guo M, Cui Z, et al. Gene therapy using adenovirus-mediated full-length anti-HER-2 antibody for HER-2 overexpression cancers. Clin Cancer Res 2006; 12: 6179-6185. 4. Wang G, Qiu J, Wang R, Krause A, Boyer JL, Hackett NR, et al. Persistent expression of biologically active anti-HER2 antibody by AAVrh.10-mediated gene transfer. Cancer Gene Ther 2010; 17: 559-570.

EDIT: A correction of the manuscript by the authors is ongoing based on the above comments. While awaiting the revision, our comments remain posted.

On 2016 Nov 27, Michael Gorn commented:

Thank you for creating this great video tutorial of our lumbar puncture (LP) technique. Video 1 is the most accurate representation of the way we performed the sonography for the study. You have captured the pertinent landmarks, especially the vascular supply of the anterior spinal space that we postulated was the main reason behind a bloody LP. This is how the concept of the Maximum Safe Depth (MSD) was developed. As you clearly demonstrated, the MSD measurements are very close in both transverse and longitudinal views, thus we used longitudinal views for convenience. Once the MSD measurement is obtained, it is marked on the needle as a safe entry depth while performing the LP. The MSD may be exceeded with caution if the needle entry level is shallow as justified by the Pythagorean equation demonstrated in the paper. However, if the entry angle is close to 90 degrees, we recommend redirecting the needle or reattempting the LP. Thank you again for your contribution.

On 2016 Nov 26, James Tsung commented:

Link to Video: http://bit.ly/2gK9osv

On 2016 Sep 16, Virginia Barbour commented:

As the Chair of COPE, I am writing to respond to the recent remarks of Dr. Horton with respect to the role and actions of COPE that he commented on in his Offline column1 highlighting the statin review by Professor Collins and colleagues, both of which were published in the issue of the 10th September. I also submitted this letter to the Lancet directly on 12th September.

COPE is an international interdisciplinary organisation, not just a UK one, whose remit is the provision of education and advice to members in questions related to publication ethics. We do have a process whereby an individual can bring to our attention complaints about journal processes, but we cannot interfere in editorial decisions and nor can we investigate the underlying issues of a complaint as we have neither the resources nor, more importantly, the appropriate level of subject–specific expertise. 

Dr Horton states that “COPE declined to act further”. This is incorrect. COPE did request details of processes at the BMJ, in accordance with our remit (http://publicationethics.org/contact-us). The guidance issued from COPE's review (I was not part of this final part of the process, having recused myself during the process because of the development of a potential conflict of interest) offered constructive criticism about how the BMJ had managed the peer review process. The BMJ had already addressed those issues following their own independent review and COPE was satisfied with the procedural changes that were implemented. 

As it is certainly not appropriate for COPE to make any specific judgment about effects on public health, COPE also recommended that Professor Collins and colleagues engaged in open dialogue on the specific issues in the medical literature. We note this has now happened with the publication of their review in The Lancet. 

Putting the correction of Dr Horton's record of events to one side, and instead looking for useful lessons, COPE would be interested in discussing Dr Horton's suggestion for an independent tribunal. It seems reasonable to assume that this tribunal would need public-funding and the ability to apply sanctions and, to a degree, become a regulator for the research community. This is not COPE's remit, but we would be interested in being part of the discussion on such an approach.

Virginia Barbour Chair, COPE

Competing interest. I'm the Chair of COPE. My decision to recuse myself from handling this issue midway through was because a colleague at PLOS (where I worked when the issue was brought to COPE) joined the BMJ.

Committee on Publication Ethics (COPE) cope_chair@publicationethics.org www.publicationethics.org

On 2016 Nov 11, James M Heilman commented:

A open access version can be read in full for free here http://journals.lww.com/academicmedicine/Abstract/publishahead/Why_Medical_Schools_Should_Embrace_Wikipedia__.98408.aspx

On 2016 Sep 26, Valter Silva commented:

This article discusses the Brazilian science based on a new resource for scientometrics called Nature Index, as well as the SJR. The 2012–2015 change in the main metric of Nature Index showed an increase of 18.9% for Brazil and currently is ranked 24th globally. From 1996 to 2015 (SJR) Brazilian science has produced more than 600 thousand citable papers, obtained more than 5 million citations, having over 400 papers with at least 400 citations and is responsible by half of Latin America publication output. Despite such numbers, there are flows in its internationalization. Much of the Brazilian science is produced by graduate students and professors gazetted, since the profession of scientist in Brazil is not a recognized position by the Ministry of Labor and Employment.

On 2016 Sep 15, Erick H Turner commented:

In addition to the two cited papers, close variations on this idea have been proposed in the following papers:

1 Walster GW, Cleary TA. A Proposal for a New Editorial Policy in the Social Sciences. The American Statistician 1970;24:16–9. doi:10.1080/00031305.1970.10478884

2 Newcombe RG. Towards a reduction in publication bias. Br Med J (Clin Res Ed) 1987;295:656–9.

3 Sridharan L, Greenland P. Editorial policies and publication bias: the importance of negative studies. Arch Intern Med 2009;169:1022–3. doi:10.1001/archinternmed.2009.100

4 Colom F, Vieta E. The need for publishing the silent evidence from negative trials. Acta Psychiatr Scand. 2011;123:91–4. doi:10.1111/j.1600-0447.2010.01650.x

5 Mirkin JN, Bach PB. Outcome-blinded peer review. Arch Intern Med 2011;171:1213–4–authorreply1214. doi:10.1001/archinternmed.2011.56

6 Turner EH. Publication bias, with a focus on psychiatry: causes and solutions. CNS Drugs 2013;27:457–68. doi:10.1007/s40263-013-0067-9

7 Smulders YM. A two-step manuscript submission process can reduce publication bias. J Clin Epidemiol Published Online First: July 2013. doi:10.1016/j.jclinepi.2013.03.023

On 2016 Nov 26, David Keller commented:

Thank you. Your findings compare with the CALM-PD study [1], which found "For subjects who consumed >12 ounces of coffee/day, the adjusted hazard ratio for the development of dyskinesia was 0.61 (95% CI, 0.37-1.01) compared with subjects who consumed <4 ounces/day." in patients at an early stage of PD. Longer follow-up should indeed be helpful in assessing whether the benefits of increased caffeine ingestion are durable, at what cost in side-effects, and whether higher doses of caffeine provide correspondingly higher benefits.

Reference

1: Wills AM, Eberly S, Tennis M, Lang AE, Messing S, Togasaki D, Tanner CM, Kamp C, Chen JF, Oakes D, McDermott MP, Schwarzschild MA; Parkinson Study Group. Caffeine consumption and risk of dyskinesia in CALM-PD. Mov Disord. 2013 Mar;28(3):380-3. doi: 10.1002/mds.25319. PubMed PMID: 23339054; PubMed Central PMCID: PMC3608707.

On 2016 Nov 25, Marcello Moccia commented:

We agree with the need for evaluating incidence and severity of dyskinesia in the long-term assessment of drug efficacy in PD. However, studies including de novo PD patients have to consider early markers of motor progression which indeed are associated with the development of dyskinesia in the long term. In view of this, we showed that the voluptuary consumption of caffeine-containing products is associated with reduced need for levo-dopa and with reduced accrual of motor symptoms. Of course, a longer follow-up will possibly confirm the positive impact of caffeine use also on dyskinesia.

On 2016 Nov 09, David Keller commented:

What effect did caffeine consumption have on the incidence or severity of dyskinesia?

In this study, higher caffeine consumption was associated with a lower rate of starting levodopa treatment and reduced motor and non-motor disability. Any treatment for Parkinson disease (PD) which delays or decreases the need for levodopa therapy should be evaluated for its propensity to hasten the onset of dyskinesia, or to worsen established dyskinesia. If the motor and non-motor benefits of caffeine are accompanied by a risk of developing dyskinesia equal to that of a levodopa regimen with equivalent benefits, then it is unclear why ingesting caffeine on a pharmacologic basis is preferable to simply initiating levodopa when it is needed.

On 2016 Sep 15, Gary Goldman commented:

Civen et al report the average HZ incidence of 12.8 cases/100,000 children aged <10 years during 2007 to 2010.¹ Since two different ascertainment sources are available for the reporting of HZ cases—schools (including preschools), and public and private healthcare providers (including hospitals)—capture-recapture techniques could have been employed to determine that the Antelope Valley project had approximately 50% case ascertainment, and thus, the true HZ figure is approximately double that reported. Interestingly, 25.6 cases/100,000, or twice the reported rate closely compares with the rate of 27.4 cases/100,000 (95% C.I. 22.7-32.7) based on 172,163 vaccinated children with overall follow-up of 446,027 person-years among children aged <12 years during 2007-2008 reported by Tseng et al.²

Civen et al report that among 10- to 19-year olds a 63% increasing trend in HZ incidence from 2000 to 2006 was documented; however, “the increased incidence could not be confidently explained.” The authors concede, “the possibility persists that children infected by wild-type VZV experienced increased rates of HZ because they were having fewer opportunities to be exposed to exogenous VZV, leading to reduced immune control of HZ.“¹ The reason that the 63% increasing trend in HZ incidence among 10- to 19-year olds has not been confidently explained is that the methodology utilized by Civen et al did not include stratifying HZ incidence rates by using two widely different cohorts: those vaccinated and those with a history of wild-type (natural) varicella. Computing a single mean HZ incidence rate of a bimodal distribution is statistically invalid and conceals the reality that the HZ incidence rate among children and adolescents with a history of wild-type varicella has an increasing trend.³ By performing such a stratified analysis, Civen et al could have tested the hypothesis that individuals with a prior history of varicella are experiencing increasing HZ incidence due to fewer exogenous exposures, and thus, reduced opportunities for boosting cell-mediated immunity to VZV.^4,5

Civen et al state, “The case for this hypothesis has weakened as studies have found no acceleration in rates of HZ among adults in the United States since the varicella vaccination was introduced, despite the fact that opportunities for varicella exposure have plummeted.” Interestingly, the same Antelope Valley surveillance project did collect HZ cases during 2000-2001 and 2006-2007 that showed statistically significant increases among adults. The Antelope Valley annual summary to the CDC demonstrates that in 2000 and 2001, HZ cases (not ascertainment corrected) reported to the project either maintained or increased in every adult 10-year age category (20–29, 30–39, . . . , 60–69 years), yielding a statistically significant difference. Reported HZ cases among adults aged 20–69 years increased 28.5%—from 158 in 2000 to 203 in 2001 (p <0.042; t = 2.95, df = 4).⁶ Again, HZ incidence rates among adults aged 50 years and older increased from 390/100,000 p-y in 2006 to 470/100,000 p-y in 2007 with a statistically significant rate ratio of 1.2 (95% CI: 1.04–1.40).⁷ A Canadian study by Marra et al concludes that "the incidence of zoster and PHN is increasing with time" and suggests "recent studies have shown an increasing incidence of herpes zoster infection, which may be related to the introduction of varicella vaccination programs in children."⁸

The United States has traded a dramatic reduction in varicella disease which in the prevaccine era accounted for only 25% of the VZV medical costs (i.e., 75% of VZV medical costs were attributed to cases of HZ) for a disproportional increase in HZ costs associated with increasing HZ incidence among adults with a history of wild-type varicella. It is an unfortunate fact that 20 years after the introduction of the varicella vaccine in the US, healthcare officials are still claiming that the mechanism of exogenous boosting “is not well understood” and “the case for this hypothesis has weakened,” when in reality, the data currently exist to understand this biological mechanism first proposed in 1965 by Dr. Robert Edgar Hope-Simpson.⁴ "Rather than eliminating varicella in children as promised, routine vaccination against varicella has proven extremely costly and has created continual cycles of treatment and disease."³

References

[1] Civen R, Marin M. Zhang J. Abraham A, Harpaz R, Mascola L. Bialek S. Update on incidence of herpes zoster among children and adolescents after implementation of varicella vaccination, Antelope Valley, CA, 2000 to 2010. Pediatr Infect Dis J. 2016 Oct; 35(10):1132-1136.Civen R, 2016

[2] Tseng HF, Smith N, Marcy SM, Sy LS, Jacobsen SJ. Incidence of herpes zoster among children vaccinated with varicella vaccine in a prepaid health care plan in the United States, 2007, 2008. Pediatr Infect Dis J 2009;28(December(12)):1069–72.Tseng HF, 2009

[3] Goldman GS and King PG. Review of the United States universal varicella vaccination program: Herpes zoster incidence rates, cost-effectiveness, and vaccine efficacy based primarily on the Antelope Valley Varicella active surveillance project data. Vaccine 2013; 31(13): 1680–1694.Goldman GS, 2013

[4] Hope-Simpson RE. The nature of herpes zoster: a long term study and a new hypothesis. Proc R Soc Med 1965; 58: 9–20.HOPE-SIMPSON RE, 1965

[5] Guzzetta G, Poletti P, Del Fava E, Ajelli M, Scalia Tomba GP, Merler S, et al. Hope-Simpson’s progressive immunity hypothesis as a possible explanation for Herpes zoster incidence data. Am J Epidemiol 2013; 177(10): 1134–1142.Guzzetta G, 2013

[6] Maupin T, Peterson C, Civen R and Mascola L. Varicella Active Surveillance Project (VASP). 2000, 2001, Annual Summary. Antelope Valley, County of Los Angeles Department of Health Services (LADHS), Acute Communicable Disease Control, Centers for Disease Control and Prevention (CDC) Cooperative Agreement No. U66/CCU911165-10.

[7] Maupin T, Peterson C, Civen R and Mascola L. Varicella Active Surveillance Project (VASP). 2006, 2007 Annual Summary. Antelope Valley , County of Los Angeles Department of Health Services (LADHS), Acute Communicable Disease Control, Centers for Disease Control and Prevention (CDC) Cooperative Agreement No. 5U01 IP000020-02/5U01 IP000020-04.

[8] Marra F, Chong M and Najafzadeh M. Increasing incidence associated with herpes zoster infection in British Columbia, Canada. BMC Infect Dis. 2016 Oct 20; 16(1):589.Marra F, 2016

On 2017 May 31, Sergio Uribe commented:

Timely and necessary reflection.

On 2016 Dec 10, Arnaud Chiolero MD PhD commented:

These findings were, unfortunately, expected. They suggest that systematic reviews should not be always regarded as the highest level of evidence; it is evident that they can be seriously biased - like any other studies.

On 2016 Nov 22, Natalie Parletta commented:

Good point re null results less likely to be published Matthew Romo. I think we also need to consider that in some instances there is a vested interest in publishing null findings, such as the systematic review on omega-3 fatty acids and cardiovascular disease (BMJ 2006; 332 doi: http://dx.doi.org/10.1136/bmj.38755.366331.2F) which did not include positive studies before 2000 (which had led to recommendations to eat fish/take fish oil for CVD) and has been critiqued for serious methodological flaws (https://www.cambridge.org/core/journals/british-journal-of-nutrition/article/pitfalls-in-the-use-of-randomised-controlled-trials-for-fish-oil-studies-with-cardiac-patients/65DDE2BD0B260D1CF942D1FF9D903239; http://www.issfal.org/statements/hooper-rebuttable). Incidentally I learned that the journal that published one of the null studies sold 900,000 reprints to a pharmaceutical company (that presumably sells statins).

On 2016 Nov 04, Matthew Romo commented:

Thank you for this very thought provoking paper. With the skyrocketing amount of systematic reviews (and meta-analyses) published, I wonder how many did not identify any evidence for their research question. If systematic reviews are research, shouldn’t we expect null results, at least once in a while? Quantifying the relative number of systematic reviews with null results (which seem to be very few) might be helpful in further understanding the degree of bias there is in published systematic reviews. After all, research should be published based on the importance of the question they seek to answer and their methodological soundness, rather than their results (Greenwald, 1993).

"Null" systematic reviews that find no evidence can be very informative for researchers, clinicians, and patients, provided that the systematic review authors leave no stone unturned in their search, as they ought to for any systematic review. For researchers, they scientifically identify important gaps in knowledge where future research is needed. For clinicians and patients, they can provide an understanding of practices that don’t have a reliable evidence base. As stated quite appropriately by Alderson and Roberts in 2000, “we should be willing to admit that ‘we don’t know’ so the evidential base of health care can be improved for future generation.”

Matthew Romo, PharmD, MPH Graduate School of Public Health and Health Policy, City University of New York

Alderson P, Roberts I. Should journals publish systematic reviews that find no evidence to guide practice? Examples from injury research. BMJ. 2000;320:376-377.

Greenwald AG. Consequences of prejudice against the null hypothesis. In: A Handbook for Data Analysis in the Behavioural Sciences, edited by Keren G, Lewis C, Hillsdale, NJ, Lawrence Erlbaum, 1993, pp419–448.

On 2016 Dec 30, Arturo Martí-Carvajal commented:

What is the degree of responsibility of either editor-in-chief of journal or peer reviewers in the publication of systematic reviews with doubtful quality?

On 2016 Sep 18, Hilda Bastian commented:

Thanks, John - that's as close we'll get, and we do agree on far more than we disagree, as ever.

I agree we should face the data, and be meticulous about it. I just don't agree that indexing has the same effect on a tagged category as it has for a filter: especially not when the filter is so broad that it encompasses the variety of terms people use to describe their work. I remain convinced that the appropriate time trend comparators are filter to filter, with triangulation of sources. I don't think it's highly likely that 90% of the RCTs are in the first 35% of tagged literature.

I don't think people should hold off publishing a systematic review that was done before deciding to fund or run a trial, until a report of the trial or its methods is published - and ideally, they would be done by different people. Intellectual conflicts of interest can be as powerful as any other. And I don't think that trialists interpreting what their trial means in the context of other evidence meets the criterion, unconflicted. Nor do I think the only systematic reviews we need are those with RCTs.

I don't think Cochrane reviews are all good quality and unconflicted - in fact, the example of a conflicted review with quality issues in my comment was a Cochrane review. I agree there is no prestigious name that guarantees quality. (It's a long time since I left the Cochrane Collaboration, by the way.) My comments aren't because I disagree that there is a flood of bad quality "systematic" reviews and meta-analyses: the title of your article is one of the many things I agree with. See for example here, here, and quite a few of my comments on PubMed Commons.

But the main reason for this reply is to add into this stream the reason I feel some grounds for optimism about something else we would both fervently agree on: the need to chip away at the problem of extensive under-reporting of clinical trials. As of January 2017, the mechanisms and incentives for reporting a large chunk of trials - those funded by NIH and affected by the FDA's scope - will change (NIH, 2016). Regardless of what happens with synthesis studies, any substantial uptick in trial reporting would be great news.

On 2016 Sep 18, John Ioannidis commented:

Dear Hilda,

thank you for all these wise thoughts. Based on prior experience, at this point in time (mid-September) the numbers for "Type of Article" meta-analysis, systematic reviews and randomized controlled trial for 2015 are likely to increase by about 10% with more complete indexing. I have taken this into account in my calculations.

I fully agree with Iain Chalmers that every trial should start and finish with a systematic review. I fervently defend upfront this concept in my paper when I say that "it is irrational not to systematically review what is already known before deciding to perform any new study. Moreover, once a new study is completed, it is useful to update the cumulative evidence", even specifically citing Iain's work. But the publication of these systematic reviews are (and should be) integral with the publication of the specific new studies. I have not counted separately the systematic reviews that are embedded within trial publications. If I were to do this, then the numbers of systematic reviews would be even higher. My proposal even goes a step further in arguing that systematic reviews and meta-analyses should be even more tightly integrated with the primary studies. Meta-analyses should become THE primary studies par excellence.

So, the answer to your question "But in an ideal world, isn't a greater number of systematic reviews than RCTs just the way it should be?" the answer is clearly "No", if we are taking about the dominant paradigm of systematic reviews of low quality that are done in isolation of the primary evidence and represent a parallel universe serving mostly its own conflicts. The vast majority of the currently published systematic reviews are not high-quality, meticulous efforts, e.g. Cochrane reviews, and they are entirely disjoint from primary studies. Cochrane reviews represent unfortunately less than 5% of this massive production. While I see that you and some other Cochrane friends have felt uneasy with the title of my paper and this has resulted in some friendly fire, I ask you to please look more carefully at this threatening pandemic which is evolving in the systematic review and meta-analysis world. Even though I trust that Cochrane is characterized by well-intentioned, non-conflicted and meticulous efforts, this bubble, which is 20-50 times larger than Cochrane, is growing next door. Let us please face the data, recognize this major problem and not try to defend ANY systematic reviews and meta-analyses as if they have value no matter what just because they happen to carry such a prestigious name.

On 2016 Sep 18, Hilda Bastian commented:

Thanks, John, for taking this so seriously - that's extremely helpful and I certainly agree with you that the rate of publication of systematic reviews is growing faster than RCTs. So the point you are talking about may well be reached at some point. Unless the rate of growth equalizes, and unless the rate of RCTs that are unpublished drops substantially: and both of those remain possible.

This comparison is much better, but it can't solve the underlying issues. Human indexing resources did not increase exponentially along with the exponential increase of literature. As of today, searching for PubMed records with 2015 in the PubMed entry date [EDAT], only 35% also have a 2015 date for completed indexing [DCOM] (which from PubMed Help looks to me the way you would check for that - but an information specialist may correct me here). That's roughly what I would expect to see: individually indexing well over a million records a year is a colossal undertaking. Being finished 2015 in just a few months while 2016 priorities are pouring in would be amazing. And we know that no process of prioritizing journals will solve this problem for trials, because the scatter across journals is so great (Hoffmann T, 2012).

So any comparison between a tagged set (RCTs) and a search based on a filter with text words (which includes systematic review or meta-analysis in the title or abstract), could generate potentially very biased estimates, no matter how carefully the results are analyzed. And good systematic reviews of non-randomized clinical trials, and indeed, other methodologies - such as systematic reviews of adverse events, qualitative studies, and more - are valuable too. Many systematic reviews would be "empty" of RCTs, but that doesn't make them useless by definition.

I couldn't agree with you more enthusiastically, though, that we still need more, not fewer, well-done RCTs, systematic reviews, and meta-analyses by non-conflicted scientists. I do add a caveat though, when it comes to RCTs. RCTs are human experimentation. It is not just that they are resource-intensive: unnecessary RCTs and some of the ways that RCTs can be "bad", can cause direct harm to participants, in a way that an unnecessary systematic review cannot. The constraints on RCTs are greater: so they need to be done on questions that matter the most and where they can genuinely provide better information. If good enough information can come from systematically reviewing other types of research, then that's a better use of scarce resources. And if only so many RCTs can be done, then we need to be sure we do the "right" ones.

For over 20 years, Iain Chalmers has argued that an RCT should not be done without a systematic review to show the RCT is justified - and there should be an update afterwards. Six years ago - he, Mike Clarke and Sally Hopewell concluded that we were nowhere near achieving that (Clarke M, 2010). The point you make about the waste in systematic reviewing underscores that point, too. But in the ideal world, isn't a greater number of systematic reviews than RCTs just the way it should be?

On 2016 Sep 17, John Ioannidis commented:

Dear Hilda,

Thank you for your follow-up comment on my reply, I always cherish your insights. I tried to get a more direct answer to the question on which we both have some residual uncertainty, i.e. whether currently published systematic reviews of trials outnumber new randomized controlled trials. So, I collected more data.

First, while we can disagree on some minor technical details, it is very clear that the annual rate has been increasing extremely fast for “meta-analyses” and very fast for “systematic reviews”, while it is rising slowly for “randomized controlled trials” types of articles. In a search as of today, the numbers per year between 2009 and 2015 using the “type of article” searches (with all their limitations) are 3243-3934-4858-6570-8192-9632-9745 for meta-analysis, 15085-17353-19378-22575-25642-29261-31609 for systematic reviews and 17879-18907-20451-22339-24538-24459-22066 for randomized controlled trials. The data are not fully complete for 2015 given that “type of article” assignments may have some delay, but comparing 2014 versus 2009 where the data are unlikely to change meaningfully with more tags, within 5-years the rate of publication of meta-analyses tripled, the rate of publication of systematic reviews doubled, while the rate of publication of randomized trials increased by only 36% (almost perfectly tracking the 33% growth of total PubMed items in the same period).

Type of article is of course not perfectly sensitive or specific in searching. So, I took a more in-depth look in a sample of 111 articles that are Type of article=“randomized controlled trial” among the 22066 published in 2015 (in the order of being retrieved by a 2015 [DP] search selecting the first and every 200th afterwards, i.e. 1, 201, 401, etc). Of the 111, 17 represent secondary analyses (the majority of secondary analyses of RCTs are not tagged as “randomized controlled trial”), 5 are protocols without results, 6 are non-human randomized studies (on cattle, barramundi etc), and 12 are not randomized trials, leaving a maximum of 71 new randomized controlled trials. I say “maximum”, because some of those 71 may actually not be randomized (e.g. there is a substantial number of “randomized” trials from China and past in-depth evaluations have shown that many/most are not really randomized even they say they are) and some others may also be secondary or duplicate publications but this is not easy to decipher based on this isolated sampling. Even if 71/111 are new RCTs, this translates to (71/111)x22060=14114 new RCTs (or articles masquerading as new RCTs) in 2015. Allowing for some missed RCTs and not yet tagged ones, it is possible that the number of new RCTs published currently is in the range of 15,000 per year. Of the 71 studies that were new RCTs or masquerading as such, only 25 had over 100 randomized participants and only 1 had over 1000 randomized participants. Clinically informative RCTs are sadly very few.

I also examined the studies tagged as Type of Article “meta-analysis” or “systematic review” or “review” published in 2015 [DP], combined with (trial* OR treatment* OR randomi*). Of the 49,166 items, I selected 84 for in-depth scrutiny (the first and every 600th afterwards, i.e. 1, 601, 1201, etc). Overall, 30 of the 84 were systematic reviews and/or meta-analyses of trials or might be masquerading as such to the average reader, i.e. had some allusion to search databases and/or search strategies and/or systematic tabulation of information. None of these 30 are affected by any of the potential caveats you raised (protocols, ACP Journal Club, split reviews, etc). Extrapolating to the total 49166, one estimates 17988 systematic reviews and/or meta-analyses of trials (or masquerading as such) in 2015. Again, allowing for missed items (e.g. pooled analyses of multiple trials conducted by the industry are not tagged as such Types of Articles), for those not yet tagged, and for a more rapid growth for such studies in 2016 than for RCTs, it is likely that the number of systematic reviews and/or meta-analyses of trials published currently is approaching 20,000 per year. If the criteria for “systematic review of trials” become more stringent (as in Page et al, 2016), this number will be substantially smaller, but will still be quite competitive against the number of new RCTs. Of course, if we focus on both stringent criteria and high quality, the numbers drop precipitously, as it happens also with RCTs.

I am sure that these analyses can be done in more detail. However, the main message is unlikely to change. There is a factory of RCTs and a far more rapidly expanding factory of systematic reviews and meta-analyses. The majority of the products of both factories are useless, conflicted, misleading or all of the above. The same applies to systematic reviews and meta-analyses for most other types of study designs in biomedical research. This does not mean that RCTs, systematic reviews, and meta-analyses are not a superb idea. If well done by non-conflicted scientists, they can provide the best evidence. We need more, not fewer, such studies that are well done and non-conflicted.

On 2016 Sep 16, Hilda Bastian commented:

Thanks, John, for the reply - and for giving us all so much to think about, as usual!

I agree that there are meta-analyses without systematic reviews, but the tagged meta-analyses are included in the filter you used: they are not additional (NLM, 2016). It also includes meta-analysis in the title, guidelines, validation studies, and multiple other terms that add non-systematic reviews, and even non-reviews, to the results.

In Ebrahim S, 2016, 191 primary trials in only high impact journals were studied. Whether they are typical of all trials is not clear: it seems unlikely that they are. Either way, hundreds of reports for a single trial is far from common: half the trials in that sample had no secondary publications, only 8 had more more than 10, and none had more than 54. Multiple publications from a single trial can sometimes be on quite different questions, which might also need to be addressed in different systematic reviews.

The number of trials has not been increasing as fast as the number of systematic reviews, but the number has not reached a definite ongoing plateau either. I have posted an October 2015 update to the data using multiple ways to assess these trends in the paper by me, Paul Glasziou, and Iain Chalmers from 2010 (Bastian H, 2010) here. Trials have tended to fluctuate a little from year to year, but the overall trend is growth. As the obligation to report trials grows more stringent, the trend in publication may be materially affected.

Meanwhile, "systematic reviews" in the filter you used have not risen all that dramatically since February 2014. For the whole of 2014, there were 34,126 and in 2015 there were 36,017 (with 19,538 in the first half of 2016). It is not clear without detailed analysis what part of the collection of types of paper are responsible for that increase. The method used to support the conclusion here about systematic reviews of trials overtaking trials themselves was to restrict the systematic review filter to those mentioning trials or treatment - “trial* OR randomi* OR treatment*”. That does not mean the review is of randomized trials only: no randomized trial need be involved at all, and it doesn't have to be a review.

Certainly, if you set the number of sizable randomized trials high, there will be fewer of them than of all possible types of systematic review: but then, there might not be all that many very sizable, genuinely systematic reviews either - and not all systematic reviews are influential (or even noticed). And yes, there are reviews that are called systematic that aren't: but there are RCTs called randomized that aren't as well. What's more, an important response to the arrival of a sizeable RCT may well be an updated systematic review.

Double reports of systematic reviews are fairly common in the filter you used too, although far from half - and not more than 10. Still, the filter will be picking up protocols as well as their subsequent reviews, systematic reviews in both the article version and coverage in ACP Journal Club, the full text of systematic reviews via PubMed Health and their journal versions (and the ACP Journal Club coverage too), individual patient data analyses based on other systematic reviews, and splitting a single systematic review into multiple publications. The biggest issue remains, though, that as it is such a broad filter, casting its net so very wide across the evidence field, it's not an appropriate comparator for tagged sets, especially not in recent years.

On 2016 Sep 16, John Ioannidis commented:

Dear Hilda,

thank you for the very nice and insightful commentary on my article. I think that my statement "Currently, probably more systematic reviews of trials than new randomized trials are published annually" is probably correct. The quote of 8,000 systematic reviews in the Page et al. 2016 article is using very conservative criteria for systematic reviews and there are many more systematic reviews and meta-analyses, e.g. there is a factory of meta-analyses (even meta-analyses of individual level data) done by the industry combining data of several trials but with no explicit mention of systematic literature search. While many papers may fail to satisfy stringent criteria of being systematic in their searches or other methods, they still carry the title of "systematic reviews" and most readers other than a few methodologists trust them as such. Moreover, the 8,000 quote was from February 2014, i.e. over 2.5 years ago, and systematic reviews' and meta-analyses' publication rates rise geometrically. Conversely, there is no such major increase in the annual rate of published randomized controlled trials. Furthermore, the quote of 38,000 trials in the Cochrane database is misleading, because it includes both randomized and non-randomized trials and the latter may be the majority. Moreover, each randomized controlled trial may have anywhere up to hundreds of secondary publications. On average within less than 5 years of a randomized trial publication, there are 2.5 other secondary publications from the same trial (Ebrahim et al. 2016). Thus the number of published new randomized trials per year is likely to be smaller than the number of published systematic reviews and meta-analyses of randomized trials. Actually, if we also consider the fact that the large majority of randomized trials are small/very small and have little or no impact, while most systematic reviews are routinely surrounded by the awe of the "highest level of evidence", one might even say that the number of systematic reviews of trials published in 2016 is likely to be several times larger than the number of sizable randomized trials published in the same time frame.

On 2016 Sep 16, Hilda Bastian commented:

There are many important issues raised in this paper on which I strongly agree with John Ioannidis. There is a lot of research waste in meta-analyses and systematic reviews, and a flood of very low quality, and he points out the contributing factors clearly. However, there are some issues to be aware of in considering the analyses in this paper on the growth of these papers, and their growth in comparison with randomized and other clinical trials.

Although the author refers to PubMed's "tag" for systematic reviews, there is no tagging process for systematic reviews, as there is for meta-analyses and trials. Although "systematic review" is available as a choice under "article types", that option is a filtered search using Clinical Queries (PubMed Help), not a tagging of publication type. Comparing filtered results to tagged results is not comparing like with like in 2 critical ways.

Firstly, the proportion of non-systematic reviews in the filter is far higher than the proportion of non-meta-analyses and non-trials in the tagged results. And secondly, full tagging of publication types for MEDLINE/PubMed takes considerable time. When considering a recent year, the gulf between filtered and tagged results widens. For example, as of December 2015 when Ioannidis' searches were done, the tag identified 9,135 meta-analyses. Today (15 September 2016), the same search identifies 11,263. For the type randomized controlled trial, the number tagged increased from 23,133 in December to 29,118 today.

In the absence of tagging for systematic reviews, the more appropriate comparisons are using filters for both systematic reviews and trials as the base for trends, especially for a year as recent as 2014. Using the Clinical Queries filter for both systematic reviews and therapy trials (broad), for example, shows 34,126 for systematic reviews and 250,195 trials. Page and colleagues estimate there were perhaps 8,000 actual systematic reviews according to a fairly stringent definition (Page MJ, 2016) and the Centre for Reviews and Dissemination added just short of 9,000 systematic reviews to its database in 2014 (PubMed Health). So far, the Cochrane Collaboration has around 38,000 trials in its trials register for 2014 (searching on the word trial in CENTRAL externally).

The number of systematic reviews/meta-analyses has increased greatly, but not as dramatically as this paper's comparisons suggest, and the data do not tend to support the conclusion in the abstract here that "Currently, probably more systematic reviews of trials than new randomized trials are published annually".

Ioannidis suggests some bases for some reasonable duplication of systematic reviews - these are descriptive studies, with many subjective choices along the way. However, there is another critical reason that is not raised: the need for updates. This can be by the same group publishing a new version of a systematic review or by others. In areas with substantial questions and considerable ongoing research, multiple reviews are needed.

I strongly agree with the concerns raised about conflicted systematic reviews. In addition to the issues of manufacturer conflicts, it is important not to underestimate the extent of other kinds of bias (see for example my comment here). Realistically, though, conflicted reviews will continue, building in a need for additional reviewers to tackle the same ground.

Systematic reviews have found important homes in clinical practice guidelines, health technology assessment, and reimbursement decision-making for both public and private health insurance. But underuse of high quality systematic reviews remains a more significant problem than is addressed here. Even when a systematic review does not identify a strong basis in favor of one option or another, that can still be valuable for decision making - especially in the face of conflicted claims of superiority (and wishful thinking). However, systematic reviews are still not being used enough - especially in shaping subsequent research (see for example Habre C, 2014).

I agree with Ioannidis that collaborations working prospectively to keep a body of evidence up-to-date is an important direction to go - and it is encouraging that the living cumulative network meta-analysis has arrived (Créquit P, 2016). That direction was also highlighted in Page and Moher's accompanying editorial (Page MJ, 2016). However, I'm not so sure how much of a solution this is going to be. The experience of the Cochrane Collaboration suggests this is even harder than it seems. And consider how excited people were back in 1995 at the groundbreaking publication of the protocol for prospective, collaborative meta-analysis of statin trials (Anonymous, 1995) - and the continuing controversy that swirls, tornado-like, around it today (Godlee, 2016).

We need higher standards, and skills in critiquing the claims of systematic reviews and meta-analyses need to spread. Meta-analysis factories are a serious problem. But I still think the most critical issues we face are making systematic reviews quicker and more efficient to do, and to use good ones more effectively and thoroughly than we do now (Chalmers I, 2009, Tsafnat G, 2014).

Disclosure: I work on projects related to systematic reviews at the NCBI (National Center for Biotechnology Information, U.S. National Library of Medicine), including some aspects that relate to the inclusion of systematic reviews in PubMed. I co-authored a paper related to issues raised here several years ago (Bastian H, 2010), and was one of the founding members of the Cochrane Collaboration.

On 2016 Oct 24, Sean Ekins commented:

this poster provides some more details http://www.slideshare.net/ekinssean/starting-small-companies-focused-on-rare-diseases

On 2016 Oct 03, Andrey Alexeyenko commented:

The counts for 2x2 table seem to be wrong. The last two terms should be:

n12 | k - x

n22 | N - [ k + d ] + x

so that n11 + n12 + n21 + n22 sum up to all genes from the genome. That is why the table is called "contingency table".

On 2016 Dec 18, Laura Williams commented:

Our online journal club discussed this paper on October 27, 2016. https://www.youtube.com/watch?v=3IKyeaBk4qM