On 2017 Apr 12, Kenneth Witwer commented:

Liu YC, 2017 reported mapping very low levels of mature plant miRNAs in a subset of public data gathered from 198 human plasma samples, concluding that this was evidence of "cross-kingdom RNAi"; however, both the authors and I observed that only one putatively foreign sequence, "MIR2910," mapped consistently and at levels above a reasonable noise threshold. No data were presented to support functional RNAi. I further noted that MIR2910 is a plant rRNA sequence, has been removed from miRBase, and also maps with 100% coverage and identity to human rRNA. In the comment below, Dr. Liu now links to unpublished predicted hairpin mapping data that were not included in the Liu YC, 2017 BMC Genomics conference article, which, like my comments, focused on mature putative xenomiRs. Dr. Liu states that mapping has been done not only to the putative MIR2910 mature sequence (as reported), but also to the predicted MIR2910 precursor hairpin sequence.

This is an interesting development, and I strongly and sincerely commend Liu et al for sharing their unpublished data in this forum. This is exactly what PubMed Commons is about: a place for scientists to engage in civil and constructive discourse.

However, examination of the new data reinforces my observation that the only consistently mapped "foreign" sequence in the Liu YC, 2017 study is a human rRNA sequence, not a plant miRNA, mature or otherwise. Beyond the 100% identity of the 21nt putative MIR2910 mature sequence with human rRNA, a 47nt stretch (80%) of the plant "pre-MIR2910" rRNA fragment aligns to human 18S rRNA with only one mismatch (lower-case), and indeed Liu et al allowed one mismatch:

Plant rRNA fragment:

UAGUUGGUGGAGCGAUUUGUCUGGUUAAUUCCGuUAACGAACGAGAC

Human rRNA fragment:

UAGUUGGUGGAGCGAUUUGUCUGGUUAAUUCCGaUAACGAACGAGAC

Dr. Liu provides the example of a plasma small RNA sequencing dataset, DRR023286, as the primary example of plant miRNA mapping, so let us examine this finding more closely. DRR023286 was by far the most deeply sequenced of the six plasma samples in the Ninomiya S, 2015 study (71.9 million reads), as re-analysed by Liu et al. Yet, like all other data examined in the Liu et al study, and despite the much deeper sequencing, DRR023286 yielded only the pseudo-MIR2910 as a clear "xenomiR" (mature or precursor). Of special note, previously reported dominant dietary plant xenomiRs such as MIR159, MIR168a, and the rRNA fragment "MIR2911" were not detected reliably, even with one mismatch.

The precursor coverage plots for DRR023286 (and less deeply sequenced datasets, for that matter), also according to the newly provided Liu et al data, show that any coverage is in the 5' 80% of the putative MIR2910 sequence: exactly the part of the sequence that matches human rRNA. The remaining 12 nucleotides at the 3' end of the purported MIR2910 precursor are conspicuously absent and never covered in their entirety. To give one example from the Liu et al data, in the deepest-sequenced DRR023286 dataset, even the single short read that includes just 11 of these 12 nucleotides has a mismatch. Furthermore, various combinations of these 3' sequences match perfectly to rRNA sequences in plant and beyond (protist, bacterial, etc.). Hence, the vanishingly small number of sequences that may appear to support a plant hairpin could just as convincingly be attributed to bacterial contamination...but we are already playing in the noise.

As noted, Liu et al allowed one mismatch to plant in their mapping and described no pre-filtering against human sequences. In the DRR023286 dataset, fully 90% of the putative mapping to plant MIR2910 included a mismatch (and thus human)...the other 10% were mostly sequences 100% identical to human.

In conclusion, the main points I raised previously have not been disputed by Liu et al:

1) numerous annotated plant miRNAs in certain plant "miRNA" databses appear to have been misannotated or the result of contamination, including some sequences reported by Liu et al that map to human and not plant;

2) the mature "MIR2910" sequence is a plant ribosomal sequence that also maps perfectly to human rRNA; and

3) the read counts for all but one putative plant xenomiR in the Liu et al study are under what one might consider a reasonable noise threshold for low-abundance RNA samples (plasma) with tens of millions of reads each.

Furthermore, the current interaction establishes a new point:

4) the plant rRNA sequence annotated by some as a "MIR2910" precursor maps almost entirely (and for all practical purposes entirely) to a human rRNA sequence.

Future, more rigorous searches for plant xenomiRs in mammalian tissues and fluids will require a pre-filtering step to exclude all sequences that map with one (or more) mismatches to all mammalian genomes/transcriptomes and preferably other possible contaminants, followed by a zero-mismatch requirement for foreign mapping.

On 2017 Apr 11, Yu-Chen Liu commented:

The authors appreciate the insightful feedbacks and agree with prospect that hypothesis derived from small RNA-seq data analysis deserve examination in skeptical views and further experimental validation. Regarding the skeptical view of Prof. Witwer on this issue, whether a specific sequence were indeed originate from plant can be validated through examining the 2’-O-methylation on their 3’ end (Chin, et al., 2016; Yu, et al., 2005). The threshold of potential copy per cell for plant miRNAs to affect human gene expression was also discussed in previous researches (Chin, et al., 2016; Zhang, et al., 2012).

Some apparent misunderstandings are needed to be clarified:

In the commentary of Prof. Witwer:

“A cross-check of the source files and articles shows that the plasma data evaluated by Liu et al were from 198 plasma samples, not 410 as reported. Ninomiya et al sequenced six human plasma samples, six PBMC samples, and 11 cultured cell lines 19. Yuan et al sequenced 192 human plasma libraries (prepared from polymer-precipitated plasma particles). Each library was sequenced once, and then a second time to increase total reads.”

Authors’ response:

First of all, the statement "410 samples" within the article was meant to the amount of runs of small RNA-seq run conducted in the referred researches. Whether multiple NGS runs conducted on same plasma sample should be count as individual experiment replicates is debatable. The analysis of each small RNA-seq run was conduct independently. The authors appreciate the kind comments for the potential confusion that can be made in this issue.

In the commentary of Prof. Witwer:

“Strikingly, the putative MIR2910 sequence is not only a fragment of plant rRNA; it has a 100% coverage, 100% identity match in the human 18S rRNA (see NR 003286.2 in GenBank; Table 3). These matches of putative plant RNAs with human sequences are difficult to reconcile with the statement of Liu et al that BLAST of putative plant miRNAs "resulted in zero alignment hit", suggesting that perhaps a mistake was made, and that the BLAST procedure was performed incorrectly.”

Authors’ response:

The precursor sequences of the plant miRNAs, including the stem loop sequences (precursor sequences) were utilized in the BLAST sequence alignment in this work. The precursor sequence of peu-MIR2910, “UAGUUGGUGGAGCGAUUUGUCUGGUUAAUUCCGUUAACGAACGAGACCUCAGCCUGCUA” was used. The alignment was not performed merely with the mature sequence, “UAGUUGGUGGAGCGAUUUGUC”. The stem loop sequences, as well as the alignment of the sequences against the plant genomes, was taken into consideration by using miRDeep2 (Friedländer, et al., 2012). As illustrated in the provided figures, sequencing reads were mapped to the precursor sequences of MIR2910 and MIR2916. As listed in the table below, a lot of sequencing reads can be aligned to other regions within the precursor sequences except the sequencing reads aligned to mature sequences. For instance, in small RNA-seq data of DRR023286, 5369 reads were mapped to peu-MIR2910, and 4010 reads were mapped to the other regions in the precursor sequences.  

miRNA | Run |Total reads | on Mature | on precursor

peu-MIR2910 | DRR023286 | 9370 | 5369 | 4010

peu-MIR2910 | SRR2105454 | 3013 | 1433 | 1580

peu-MIR2914 | DRR023286 | 1036 | 19 | 1017

peu-MIR2916 |SRR2105342 | 556 | 227 | 329

(Check the file MIR2910_in_DRR023286.pdf, MIR2910_in_SRR2105454.pdf, MIR2914_in_DRR023286 and MIR2916_in_SRR2105342.pdf)

The pictures are available in the URL:

https://www.dropbox.com/sh/9r7oiybju8g7wq2/AADw0zkuGSDsTI3Aa_4x6r8Ua?dl=0

As described in the article, all reported reads mapped onto the plant miRNA sequences were also mapped onto the five conserve plant genomes. Within the provided link a compressed folder file “miRNA_read.tar.gz” is available. Results of the analysis through miRDeep2, were summarized in these pdf files. Each figure file was named according to the summarized reads, sequence run and the mapped plant genome. For example, reads from the run SRR2105181 aligned onto both Zea mays genome and peu-MIR2910 precursor sequences are summarized in the figure file “SRR2105181_Zea_mays_peu-MIR2910.pdf”.

In the commentary of Prof. Witwer:

“Curiously, several sequences did not map to the species to which they were ascribed by the PMRD. Unfortunately, the PMRD could not be accessed directly during this study; however, other databases appear to provide access to its contents.”

Authors’ response:

All the stem loop sequences of plant miRNAs were acquired from the 2016 updated version of PMRD (Zhang, et al., 2010), which was not properly referred. The used data were provided in the previously mentioned URL.

In the commentary of Prof. Witwer:

“Counts were presented as reads per million mapped reads (rpm). In contrast, Liu et al appear to have reported total mapped reads in their data table. Yuan et al also set an expression cutoff of 32 rpm (log2 rpm of 5 or above). With an average 12.5 million reads per sample (the sum of the two runs per library), and, on average, about half of the sequences mapped, the 32 rpm cutoff would translate to around 200 total reads in the average sample as mapped by Liu et al.”

Authors’ response:

Regarding the concern of reads per million mapped reads (rpm) threshold, the author appreciate the kind remind of the need to normalize sequence reads count into the unit in reads per million mapped reads (rpm) for proper comparison between samples of different sequence depth. However the comparison was unfortunately not conducted in this work. Given the fact that the reads were mapped onto plant genome instead of human genome, the normalization would be rather pointless, considering the overall mapped putative plant reads only consist of ~3% of the overall reads. On the other hand, the general amount of cell free RNA present in plasma samples was meant to be generally lower than within cellar samples (Schwarzenbach, et al., 2011).

Reference

Chin, A.R., et al. Cross-kingdom inhibition of breast cancer growth by plant miR159. Cell research 2016;26(2):217-228.

Friedländer, M.R., et al. miRDeep2 accurately identifies known and hundreds of novel microRNA genes in seven animal clades. Nucleic acids research 2012;40(1):37-52.

Schwarzenbach, H., Hoon, D.S. and Pantel, K. Cell-free nucleic acids as biomarkers in cancer patients. Nature Reviews Cancer 2011;11(6):426-437.

Yu, B., et al. Methylation as a crucial step in plant microRNA biogenesis. Science 2005;307(5711):932-935.

Zhang, L., et al. Exogenous plant MIR168a specifically targets mammalian LDLRAP1: evidence of cross-kingdom regulation by microRNA. Cell research 2012;22(1):107-126.

Zhang, Z., et al. PMRD: plant microRNA database. Nucleic acids research 2010;38(suppl 1):D806-D813.

On 2017 Apr 07, Kenneth Witwer commented:

Caution is urged in interpreting this conference article, as described in more detail in my recent commentary. For careful analysis of this issue, using greater numbers of studies and datasets and coming to quite the opposite conclusions, see Kang W, 2017 and Zheng LL, 2017. Here, Liu et al examined sequencing data from two studies of a total of 198 plasma samples (not 410 as reported). Although no canonical plant miRNAs were mapped above a reasonable background threshold, one rRNA degradation fragment that was previously and erroneously classified as a plant miRNA, MIR2910, was reported at relatively low but consistent counts. However, this rRNA fragment is found in human 18S rRNA and is thus most simply explained as part of the human degradome. The other reportedly detected plant miRNAs were mostly found in a small minority of samples and in those were mapped at average read counts of less than one per million. These sequences may be amplification, sequencing, or mapping errors, since reads were mapped directly to plant (with one mismatch allowed) with no pre-filtering against mammalian genomes/transcriptomes. Several purported plant sequences, e.g., ptc-MIRf12412-akr and ptc-MIRf12524-akr, map perfectly to human sequences but do not appear to map to Populus or to other plants, suggesting that the plant miRNA database used by the authors and published in 2010 may include some human sequences. This is not a surprise, given pervasive low-level contamination in sequencing data, as reported by many authors.

Of course, even if some of the mapped sequences were genuine plant RNAs, they would be present in blood at greatly subhormonal levels unlikely to affect biological processes. No evidence of function is provided, apart from in silico predictions of human targets of the putative MIR2910 sequence, which, as noted above, is a human sequence. Thus, the titular claim of "evidences of cross-kingdom RNAi" is wholly unsupported. Overall, the results of this study corroborate the findings of Kang W, 2017 and previous studies: that dietary xenomiR detection is likely artifactual.

On 2017 Apr 07, Atanas G. Atanasov commented:

A very interesting and innovative research topic… I have featured this manuscript at: http://healthandscienceportal.blogspot.com/2017/04/chronic-diseases-and-aging-potential.html

On 2017 Jun 05, Frances Cheng commented:

Immobility in mice, calm or stressed?

Frances Cheng, PhD; Ingrid Taylor, DVM; Emily R Trunnell, PhD

People for the Ethical Treatment of Animals

This paper by Yackle, et al. claims to have found a link between breathing and calmness in mice. However, the conclusions made by the authors leave several critical questions unanswered.

Mice are naturally inquisitive and the expression of exploratory behavior is generally interpreted as good welfare. Conversely, being motionless or less exploratory is typically thought to be indicative of stress, pain, or poor welfare. There is no established relationship between calmness and sitting still; in fact the literature would likely attribute time spent immobile to anxiety in this species. Similarly, the relationship between grooming and calmness is not clear. Grooming can be elicited by both stressful and relaxing situations, and as such is problematic to use as an absolute marker of stress levels. In some cases, grooming can be a stress reliever and restraint stress can increase grooming (1). A study by Kaleuff and Tuohima attempted to differentiate between stress grooming and relaxed grooming, stating: “While a general pattern of self-grooming uninterrupted cephalocaudal progression is normally observed in no-stress (comfort) conditions in mice and other rodents, the percentage of ‘incorrect’ transitions between different stages and the percentage of interrupted grooming bouts may be used as behavioural marker of stress" (2). Indeed the preBötC ablated mouse in this supplementary video (http://science.sciencemag.org/content/sci/suppl/2017/03/29/355.6332.1411.DC1/aai7984s1.mp4) appears to be less active, but without other objective measurements, it is a leap to conclude that this mouse is calm.

The chamber used to measure the animals’ behavior is extremely small and inadequate for observing mouse behavior and making conclusions about calmness or other emotions, particularly when the differences in behavior between the two mice being compared are very subtle, as they are here. In addition, simply being in a chamber of this size could potentially be restraining and stress-inducing. A larger chamber would allow for more traditional measures of calmness and anxiety, such as exploratory behavior, where the amount of time the mouse spends along the wall of the chamber versus the amount of time he or she leaves the safety of the walls to explore the center area is measured and scored (the Open Field test).

As mentioned, sitting still does not necessarily dictate calmness, and in many behavioral paradigms, immobility is thought to be an outward sign of anxiety or distress. The authors mention that they observe different breathing rates associated with different behaviors, e.g., faster during sniffing and slower during grooming; however, observed breathing rate alone cannot be used as the sole measure to associate an emotion with a behavior. Consider that humans under stress can hyperventilate when sitting still. It would be more informative, and more applicable to calmness, to know whether or not ablation of Cdh9/Dbx1 double-positive preBötC neurons would influence one’s ability to control their breathing and potentially to breathe slower during a psychologically stressful situation, rather than how the ablation impacts breathing coupled with normal physiological functions.

It is not clear if the experimental group is physiologically capable of breathing faster in response to external stimuli. Not being able to do so—in other words being programmed to breathe a certain way—could be distressing. The lack of compensatory respiration mechanisms, such as increased respiration in unknown, potentially dangerous situations, could affect prey species such as mice in ways that have not been previously characterized.

The experimental groups were born with full use of the Cdh9/Dbx1 double-positive preBötC neurons. These neurons were ablated in adult animals. If these animals did not have a full range of control of their breathing after ablation, they might have experienced unpleasant psychological reactions to the forced change in breathing pattern, which could be distressing.

In the Methods section, the authors did not specify whether or not the behavioral experiment was performed during the mice's light or dark cycle. From the Supplementary video, linked above, the artificial lighting of the indoor facility also makes this determination impossible. As you may know, mice are nocturnal. Conducting behavioral tests during the light cycle, when the mice would normally be sleeping, can lead to dramatically different results (3,4). Interruption of a rodent’s normal sleeping period reduces welfare and increases stress (5,6). It has been recommended that for behavioral phenotyping of genetically engineered mice, dark-phase testing allows researchers to better discriminate these strains against wild-type animals and provides superior outcomes (7).

To fully assess calmness or stress, one can measure physiological parameters such as hormone levels or heart rate, to name a few. However, the authors did not examine any measure of stress beyond breathing rate, which they artificially manipulated, not even to measure the baseline stress level between groups. The use of theta rhythm as secondary external validation for emotion further supports our concerns that the authors have drawn a broad conclusion based on rather tenuous connections. The relationship between theta rhythm and arousal may depend entirely on locomotion. As noted by Biskamp and colleagues, “The power of hippocampal theta activity, which drives theta oscillations in the mPFC, depends on locomotion and is attenuated when animals remain immobile” (8). The authors conclude that mice are “calm” for simply sitting still, a behavior that has in most other cases been attributed to decreased well-being.

For the reasons listed above, we are concerned that the authors may have drawn premature and/or incorrect conclusions regarding the relative “calmness” of the mice with preBötC ablation. Importantly, the authors claim as a justification for their work that this data may be useful in understanding the effects of pranayama yoga on promoting “mental calming and contemplative states”. However, the practice of pranayama includes not only controlled breathing but also mental visualization and an increased emphasis on abdominal respiration. There are also periods when the breath is held deliberately. It cannot be assumed the various components of pranayama can individually achieve a calmer state in humans, and, crucially, these components cannot be modeled or replicated in animals.

References

1) S.D. Paolo et al., Eur J Pharmacol., 399, 43-47 (2000).

2) A.V. Kaleuff, P. Tuohimaa, Brain Res. Protoc., 13, 151-158 (2004).

3) A. Nejdi, J. M. Gustavino, R. Lalonde, Physiol. Behav., 59, 45-47 (1995).

4) A. Roedel, C. Storch, F. Holsboer, F. Ohl, Lab. Anim., 40, 371-381 (2006).

5) U. A. Abou-Ismail, O. H. P. Burman, C. J. Nicol, M. Mendl, Appl. Anim. Behav. Sci., 111, 329-341 (2008).

6) U. A. Abou-Ismail, R. A. Mohamed, S. Z, El-Kholya, Appl. Anim. Behav. Sci., 162, 47-57 (2015).

7) S. M. Hossain, B. K. Y. Wong, E. M. Simpson, Genes Brain Behav., 3, 167-177 (2004).

8) J. Biskamp, M. Bartos, J. Sauer, Sci. Rep., 7, 45508 (2017).

On 2017 Apr 02, Atanas G. Atanasov commented:

Thanks a lot for the excellent overview; I have featured the manuscript at: http://healthandscienceportal.blogspot.com/2017/04/recent-advances-in-parkinsons-disease.html

On 2017 Nov 10, Thomas Heston commented:

This is an interesting concept which could improve scientific research and trust in science. One possible shortcoming of their proposal is that they propose a private network as opposed to an open network with no central authority as proposed in the Blockchain-based scientific study (Digit Med 2017;3:66-8). These concepts of combining blockchain technology with smart contracts are a step in the right direction towards making research studies more reproducible, reliable, and trusted.

On 2017 Apr 01, Lydia Maniatis commented:

Last sentence of abstract: "Our findings suggest participants integrate shape, motion, and optical cues to infer stiffness, with optical cues playing a major role for our range of stimuli."

The authors offer no criterion for "range of stimuli," even though they clearly limit their conclusions to this undefined set. This means that. if one wanted to attempt a replication, it would not be clear what "range of stimuli" would constitute a valid attempt. The relevance of this point can be appreciated in the context of statements like: "Compared with previous studies, we find a much less pronounced effect of shape cues compared with material cues (Han & Keyser, 2015, 2016; Paulun et al., 2017)." Speculation as to the reasons for this discrepancy are moot if we can't circumscribe our stimulus set in a theoretically clear way.

Also, the terms "shape, motion, and optical cues," as they are used by the authors, reflect an unproductive failure to distinguish between perceived and physical properties. Relevant physical properties of a stimulus are limited to the retinal stimulation it produces. The correct title for this paper would be "Inferring the stiffness of unfamiliar objects from their inferred surface properties, shapes, and motions."

Instead, the authors are treating stiffness as an inference and the rest as objective fact. (Not that thinking about perceptual qualities like stiffness, which seem more indirectly* inferred than the others, isn't interesting in itself, but the lines between perception and physics, and the relationships between them, shouldn't be blurred).

*Having said this, I don't think it's actually appropriate to characterize any perceived quality as more or less indirect than others. Even the seemingly simplest things - such as extent (which includes amodal completion), or lightness (which includes double layers, subjective contours), are not in any sense read directly off of the retinal stimulation.

The problem of confusing perceived and objective properties is the more acute given that the investigators aren't using real objects, but objects that rendered by a third-party computer program. "

"The render engine used to generate the final images was Maxwell 3.0.1.3 (NextLimit Technologies, Madrid, Spain).... Specifically, they were designed to approximate the following materials: black marble, white marble, porcelain, nickel, concrete paving, cement, ceramic, steel, copper, light wood, dark wood, silvered glass, glass, stone, leather, wax, gelatine, cardboard, plastic, paper, latex, cork, ice cream, lichen, waffle, denim, moss, and velvet. Some of these materials were downloaded or based on downloads from the Maxwell free resources library (http://resources.maxwellrender.com), and others were designed by us."

The authors are skipping all the good parts. What are the theoretical underpinnings of what are essentially assumptions about what various computer images will look like? Why is Maxwell's rendering of "velvet" equivalent, in terms of the retinal stimulation it generates, with real velvet? What are the criteria of a valid rendering of all of these perceived qualities and substances?

The criteria are empirical (see below), but loose. It is not clear that they are statistically valid, or how this could be assessed:

"Finally, Supplementary Figure S2 summarizes the results of the free material-naming task. Generally, they show that most of our renderings yielded compelling impressions of realistic materials that observers were able to reliably classify. In the following, the naming results were used to decide on the materials to test in Experiments 3 and 4 by choosing only materials that were identified as the same material by at least 50% of participants (see Stimuli section of Experiment 3)."

Fifty percent agreement seems like a pretty low bar. Why not at least 51% (which would still be low). Why not shoot for 100%? Is normal inter-individual variability in perception of materials this low in real-life? Or are the renderings generally inadequate? Even poor pictorial renderings of materials can contain cues - e.g. wood grain - which could produce seemingly clear answers that don't really reflect a valid percept in all the particulars. The very brief description of the naming task doesn't make it clear whether or not it was a forced answer, i.e. whether or not participants were allowed to say "not sure," which seems relevant.

On 2017 Apr 05, Gwinyai Masukume commented:

The authors state that South Africa is the “country with the highest global incidence of HIV/AIDS.”

This is an oversight because both Swaziland and Lesotho have an estimated HIV incidence rate among adults (15-49) greater than South Africa’s. The incidence rates as of 2015, the most recent available from http://aidsinfo.unaids.org/, are 1.44 for South Africa, 1.88 for Lesotho and 2.36 for Swaziland.

This translates into approximately 380 000 new HIV infections per year for South Africa, 18 000 for Lesotho and 11 000 for Swaziland. South Africa has a much larger population, about 55 million people compared to Lesotho’s of about 2 million and to Swaziland’s of about 1.5 million https://www.cia.gov/library/publications/the-world-factbook/rankorder/2119rank.html#sf.

Although the absolute numbers of new HIV infections is higher for South Africa, both Lesotho and Swaziland, for their population sizes, have disproportionately more new HIV infections (incidence) than South Africa.

On 2017 May 09, Kenneth J Rothman commented:

Lappe et al. (1) reported that women receiving vitamin D and calcium supplementation had 30% lower cancer risk than women receiving placebo after four years (hazard ratio (HR)=0.70, 95% confidence interval (CI): 0.47 to 1.02). Remarkably, they interpreted this result as indicating no effect. So did the authors of the accompanying editorial (2), who described the 30% lower risk for cancer as “the absence of a clear benefit,” because the P-value was 0.06. Given the expected bias toward a null result in a trial that comes from non-adherence coupled with an intent-to-treat analysis (3), the interpretation of the authors and editorialists is perplexing. The warning issued last year by the American Statistical Association (ASA) (4) about this type of misinterpretation of data should be embraced by researchers and journal editors. In particular, the ASA stated: “Scientific conclusions …should not be based only on whether a p-value passes a specific threshold.” Editors in particular ought to guide their readership and the public at large to avoid such mistakes and foster more responsible interpretation of medical research.

EE Hatch, LA Wise

Boston University School of Public Health

KJ Rothman

Research Triangle Institute & Boston University School of Public Health

References

(1) Lappe J,Watson P, Travers-Gustafson D, et al. Effect of vitamin D and calcium supplementation on cancer incidence in older women. JAMA. 2017; 317:1234-1243. doi:10.1001/jama.2017.2115

(2) Manson JE, Bassuk SS, Buring JE. Vitamin D, Calcium, and Cancer. Approaching Daylight? JAMA 2017; 317:1217-1218.

(3) Rothman KJ. Six persistent research misconceptions. J Gen Intern Med 2014; 29:1060-1064. doi: 10.1007/s11606-013-2755-z

(4) ASA statement on statistical significance and P-values. Am Stat. 2016. doi:10.1080/ 00031305.2016.1154108.

On 2017 Jun 01, JOANN MANSON commented:

We are writing in response to the comment by EE Hatch, LA Wise, and KJ Rothman that was posted on PubMed Commons on May 9. The authors questioned our interpretation [1] of the key finding of the recent randomized trial by Lappe et al. [2], asserting that we relied solely on the p-value of 0.06 and noting that “Scientific conclusions…should not be based only on whether a p-value passes a specific threshold.” However, the p-value in isolation was not the basis for our interpretation of this trial’s results or our conclusion regarding the effectiveness of vitamin D supplementation as a chemopreventive strategy. As we stated in our editorial, “...the absence of a clear benefit for this endpoint [in the Lappe et al. trial] is in line with the totality of current evidence on vitamin D and/or calcium for prevention of incident cancer..... [F]indings from observational epidemiologic studies and randomized clinical trials to date have been inconsistent. Previous trials of supplemental vitamin D, albeit at lower doses ranging from 400 to 1100 IU/d and administered with or without calcium, have found largely neutral results for cancer incidence; a 2014 meta-analysis of 4 such trials [3-6] with a total of 4333 incident cancers among 45,151 participants yielded a summary relative risk (RR) of 1.00 (95% CI, 0.94-1.06) [7]. Similarly, previous trials of calcium administered with or without vitamin D have in aggregate demonstrated no effect on cancer incidence, with a 2013 meta-analysis reporting a summary RR of 0.95 (0.76-1.18) [8].” (Parenthetically, we note that, in aggregate, vitamin D trials do find a small reduction in cancer mortality [summary RR=0.88 (0.78-0.98)] [7], but, as stated in our editorial, “[t]he modest size, relatively short duration, and relatively small numbers of cancers in the [recent Lappe et al.] trial … preclude[d] robust assessment” of the cancer mortality endpoint.) If the commenters believe that a p-value of 0.06 in the context of the generally null literature (at least for the endpoint of cancer incidence) should be interpreted as a positive finding, then where do they draw the line? A p-value of 0.07, 0.10, 0.20, or elsewhere? Large-scale randomized trials of high-dose supplemental vitamin D are in progress and are expected to provide definitive answers soon regarding its utility for cancer prevention.

--JoAnn E. Manson, MD, DrPH1,2, Shari S. Bassuk, ScD1, Julie E. Buring, ScD1,2

1Division of Preventive Medicine, Brigham and Women's Hospital, Harvard Medical School, Boston<br> 2Department of Epidemiology, Harvard T.H. Chan School of Public Health, Boston

References

1. Manson JE, Bassuk SS, Buring JE. Vitamin D, calcium, and cancer: approaching daylight? JAMA 2017;317:1217-8.
2. Lappe J, Watson P, Travers-Gustafson D, et al. Effect of vitamin D and calcium supplementation on cancer incidence in older women: a randomized clinical trial. JAMA 2017;317:1234-43.
3. Trivedi DP, Doll R, Khaw KT. Effect of four monthly oral vitamin D3 (cholecalciferol) supplementation on fractures and mortality in men and women living in the community: randomised double blind controlled trial. BMJ 2003;326:469.
4. Wactawski-Wende J, Kotchen JM, Anderson GL, et al. Calcium plus vitamin D supplementation and the risk of colorectal cancer. N Engl J Med 2006;354:684-96.
5. Lappe JM, Travers-Gustafson D, Davies KM, Recker RR, Heaney RP. Vitamin D and calcium supplementation reduces cancer risk: results of a randomized trial. Am J Clin Nutr 2007;85:1586-91.
6. Avenell A, MacLennan GS, Jenkinson DJ, et al. Long-term follow-up for mortality and cancer in a randomized placebo-controlled trial of vitamin D3 and/or calcium (RECORD trial). J Clin Endocrinol Metab 2012;97:614-22.
7. Keum N, Giovannucci E. Vitamin D supplements and cancer incidence and mortality: a meta-analysis. Br J Cancer 2014;111:976-80.
8. Bristow SM, Bolland MJ, MacLennan GS, et al. Calcium supplements and cancer risk: a meta-analysis of randomised controlled trials. Br J Nutr 2013;110:1384-93.

On 2017 May 09, Kenneth J Rothman commented:

Lappe et al. (1) reported that women receiving vitamin D and calcium supplementation had 30% lower cancer risk than women receiving placebo after four years (hazard ratio (HR)=0.70, 95% confidence interval (CI): 0.47 to 1.02). Remarkably, they interpreted this result as indicating no effect. So did the authors of the accompanying editorial (2), who described the 30% lower risk for cancer as “the absence of a clear benefit,” because the P-value was 0.06. Given the expected bias toward a null result in a trial that comes from non-adherence coupled with an intent-to-treat analysis (3), the interpretation of the authors and editorialists is perplexing. The warning issued last year by the American Statistical Association (ASA) (4) about this type of misinterpretation of data should be embraced by researchers and journal editors. In particular, the ASA stated: “Scientific conclusions …should not be based only on whether a p-value passes a specific threshold.” Editors in particular ought to guide their readership and the public at large to avoid such mistakes and foster more responsible interpretation of medical research.

EE Hatch, LA Wise

Boston University School of Public Health

KJ Rothman

Research Triangle Institute & Boston University School of Public Health

References

(1) Lappe J,Watson P, Travers-Gustafson D, et al. Effect of vitamin D and calcium supplementation on cancer incidence in older women. JAMA. 2017; 317:1234-1243. doi:10.1001/jama.2017.2115

(2) Manson JE, Bassuk SS, Buring JE. Vitamin D, Calcium, and Cancer. Approaching Daylight? JAMA 2017; 317:1217-1218.

(3) Rothman KJ. Six persistent research misconceptions. J Gen Intern Med 2014; 29:1060-1064. doi: 10.1007/s11606-013-2755-z

(4) ASA statement on statistical significance and P-values. Am Stat. 2016. doi:10.1080/ 00031305.2016.1154108.

On 2017 Sep 20, MICHAEL BEETS commented:

Nice work

On 2017 Sep 19, Helmi BEN SAAD commented:

The correct names of the authors are: "Khemiss M, Ben Khelifa M, Ben Rejeb M, Ben Saad H".

On 2017 Sep 19, Helmi BEN SAAD commented:

The correct name of the last author is "Ben Saad H".

On 2017 Sep 19, Helmi BEN SAAD commented:

The correct name of the last author is "Ben Saad H".

On 2017 Sep 19, Helmi BEN SAAD commented:

The correct name of the last author is "Ben Saad H".

On 2017 May 19, Donald Forsdyke commented:

THE VIRUS-VIRUS ARMS RACE

For commentary on this paper please see ArXiv preprint (1). For further discussion see commentary on a BioRxiv preprint (2).

(1) Forsdyke DR (2016) Elusive preferred hosts or nucleic acid level selection? ArXiv Preprint (https://arxiv.org/abs/1612.02035).

(2) Shmakov SA, Sitnik V, Makarova KS, Wolf YI, Severinov KV, Koonin EV (2017) The CRISPR spacer space is dominated by sequences from the species-specific mobilome. BioRxiv preprint (http://biorxiv.org/content/early/2017/05/12/137356).

On 2017 Jun 12, Bastian Fromm commented:

Summary The author describes the results of a combined smallRNA sequencing and blasting approach in Taenia ovis. Specifically RNA was retrieved from Tov metacercaria and then mapped to the genome of T. solium. Mapping reads are then blasted against miRBase and so the author describes 34 miRNAs as present in Tov.

Major problems

1. The author uses miRBase as reference for cestode miRNAs although it is very outdated (last update 2014). The author should rather have used available literature for comparisons (1-9).
2. Consequently (?) the author fails to acknowledge his results in the light of standard work in the field of miRNA evolution in flatworms (10-12) and to draw conclusions about the completeness of his predictions.
3. The approach of mapping a smallRNA sequencing library of a given species against another is problematic and I cannot understand why no the author does not at least try to use classical PCR to confirm loci.

Minor problems 1) page 3 line 61 author should make sentence more clear. It looks like author removed all reads that had adapter sequences. Recommendation 1) Author should get all available PRE-sequences for cestodes and ma his Tov reads with liberal settings to them and report results.

1. Jiang, S., Li, X., Wang, X., Ban, Q., Hui, W. and Jia, B. (2016) MicroRNA profiling of the intestinal tissue of Kazakh sheep after experimental Echinococcus granulosus infection, using a high-throughput approach. Parasite, 23, 23.
2. Kamenetzky, L., Stegmayer, G., Maldonado, L., Macchiaroli, N., Yones, C. and Milone, D.H. (2016) MicroRNA discovery in the human parasite Echinococcus multilocularis from genome-wide data. Genomics, 107, 274-280.
3. Macchiaroli, N., Cucher, M., Zarowiecki, M., Maldonado, L., Kamenetzky, L. and Rosenzvit, M.C. (2015) microRNA profiling in the zoonotic parasite Echinococcus canadensis using a high-throughput approach. Parasit Vectors, 8, 83.
4. Jin, X., Guo, X., Zhu, D., Ayaz, M. and Zheng, Y. (2017) miRNA profiling in the mice in response to Echinococcus multilocularis infection. Acta tropica, 166, 39-44.
5. Bai, Y., Zhang, Z., Jin, L., Kang, H., Zhu, Y., Zhang, L., Li, X., Ma, F., Zhao, L., Shi, B. et al. (2014) Genome-wide sequencing of small RNAs reveals a tissue-specific loss of conserved microRNA families in Echinococcus granulosus. BMC genomics, 15, 736.
6. Cucher, M., Prada, L., Mourglia-Ettlin, G., Dematteis, S., Camicia, F., Asurmendi, S. and Rosenzvit, M. (2011) Identification of Echinococcus granulosus microRNAs and their expression in different life cycle stages and parasite genotypes. International journal for parasitology, 41, 439-448.
7. Ai, L., Xu, M.J., Chen, M.X., Zhang, Y.N., Chen, S.H., Guo, J., Cai, Y.C., Zhou, X.N., Zhu, X.Q. and Chen, J.X. (2012) Characterization of microRNAs in Taenia saginata of zoonotic significance by Solexa deep sequencing and bioinformatics analysis. Parasitology research, 110, 2373-2378.
8. Wu, X., Fu, Y., Yang, D., Xie, Y., Zhang, R., Zheng, W., Nie, H., Yan, N., Wang, N., Wang, J. et al. (2013) Identification of neglected cestode Taenia multiceps microRNAs by illumina sequencing and bioinformatic analysis. BMC veterinary research, 9, 162.
9. Ai, L., Chen, M.-X., Zhang, Y.-N., Chen, S.-H., Zhou, X.-N. and Chen, J.-X. (2014) Comparative analysis of the miRNA profiles from Taenia solium and Taenia asiatica adult. African Journal of Microbiology Research, 8, 895-902.
10. Fromm, B., Worren, M.M., Hahn, C., Hovig, E. and Bachmann, L. (2013) Substantial Loss of Conserved and Gain of Novel MicroRNA Families in Flatworms. Molecular biology and evolution, 30, 2619-2628.
11. Cai, P., Gobert, G.N. and McManus, D.P. (2016) MicroRNAs in Parasitic Helminthiases: Current Status and Future Perspectives. Trends Parasitol, 32, 71-86.
12. Fromm, B., Ovchinnikov, V., Hoye, E., Bernal, D., Hackenberg, M. and Marcilla, A. (2016) On the presence and immunoregulatory functions of extracellular microRNAs in the trematode Fasciola hepatica. Parasite immunology.

On 2017 May 16, Michael Tatham commented:

Is CoAlation biologically relevant or a non-functional by-product of the chemical reaction between CoA and cysteine thiols in proximal proteins under certain redox conditions?

Firstly, in my opinion the work described here is technically sound. The development of the specific antibody for CoA, and the mass spectrometric method to detect the modification on peptides are key tools in the analysis of any post-translational modification. However, there is a risk when using these super-sensitive methods, that one can detect vanishingly small amounts of modified peptides, which inevitably calls relevance into question. More specifically, modern mass-spectrometry based proteomics in combination with peptide-level enrichment of modified species has allowed us to identify modification sites in the order of tens of thousands for phosphorylation, ubiquitination, acetylation and SUMOylation (as of May 2017). For these fields, the onus of the researcher has very quickly shifted from identification of sites, to evidence for biological meaning. In short, the question is no longer “Which proteins?”, but “Why?”.

Taking acetylation as an example: Phosphositeplus (www.phosphosite.org) lists over 37000 acetylation sites, the majority identified via MS-based proteomics where acetylated peptides have been enriched using acetylated lysine specific antibodies. However, further work investigating endogenous stoichiometry (or site occupancy) of acetylated lysines has revealed that the vast majority are below 1%. Meaning, for most sites, less than 1% of the pool of a protein actually has an acetyl group on a particular lysine (see https://www.ncbi.nlm.nih.gov/pubmed/26358839 and https://www.ncbi.nlm.nih.gov/pubmed/24489116). This clearly calls into question the ability of acetylation to drastically alter the function of most of the proteins identified as ‘targets’.

A very interesting hypothesis is emerging, whereby many of the identified sites of acetylation are not mediated by the specific transfer of acetyl groups via acetyl-transferase enzymes in cells, but are direct acceptors of acetyl groups from reactive chemicals such as acetyl-CoA, or acetyl-phosphate (an earlier review can be found here https://www.ncbi.nlm.nih.gov/pubmed/24725594). This is termed, non-enzymatic, or chemical modification.

Intriguingly, this proximity-based direct modification process may not be restricted to non-enzymatic modification systems. In fact the majority of enzyme-catalysed cellular post-translational modifications involve highly reactive intermediates (such as thioester-bonded ubiquitin or ubiquitin-like modifiers to E1 or E2 enzymes), which can modify lysines in absence of the specificity-determining enzymes (E3 ligases). So it follows that ‘unintended’ modifications can occur for any biologically relevant post-translational modification simply by spatial proximity. This actually also fits with the acetylation site occupancy studies that showed (relatively) higher occupancy in proteins that are themselves involved in acetylation dynamics. Couple these theories with the exquisitely sensitive detection methods used in modern proteomics studies, and we have the potential to create huge lists of modification sites where the proportion with true biological relevance is unknown.

Where does this all fit in with this work describing post-translational modification of cellular proteins with CoA? Reviewing these data bearing the above in mind, it seems the simplest explanation is that non-enzymatic CoAlation occurs in cells when the redox potential has shifted to tip the balance in favour of reaction of CoA with cysteine thiols in proximal proteins. Removal of oxidising agents would allow the balance to revert to more reducing conditions, and so reversal of the CoAlation. The data presented in this paper support this idea as CoAlation is redox-dependent and ‘targets’ proteins that are known to interact with CoA in the cell.

In short, as with many of the published post-translational modification proteomes, much needs to be done to give biological credibility to sites of CoAlation. In particular occupancy calculations and protein-specific evidence that CoAlation regulates function in vivo, will go a long way to putting the notion of biological relevance beyond reasonable doubt. Until then we should consider the possibility that in many cases, post-translational modifications identified by modern methods have the potential to be the unintended consequence of interactions between reactive molecules and nearby proteins. It is worth noting that such a situation does not exclude biological relevance, but it makes finding any very challenging.

On 2017 Apr 05, Leonie Brose commented:

Correction to Figure: The parts of figure 1 are in the wrong place so that the results and the figure legend refer to the wrong bar chart; the chart shown as 1c (workplaces) should be at the top of the figure as 1a, thereby shifting 1a (homes) to 1b, and 1b (extending law) to 1c. In the legend for 1b, ‘by socio-economic status’ is incorrect and should be omitted.

On 2017 Mar 28, Peter Hajek commented:

After stop-smoking treatment, smokers who quit successfully have no need to use e-cigarettes and so treatment successes are concentrated in the group that did not vape post-treatment. Quit rates are of course higher in this group.

A more informative analysis would compare quit rates at one year in people who failed to stop smoking after treatment and who did and did not try vaping during the follow-up period (though even this would face the problem of self-selection).

The results as reported just show that people who fail to stop smoking with other methods are more likely to try e-cigarettes than those who quit smoking successfully.

It is unfortunate that the Conclusions fail to point this out and instead indicate that vaping undermined quitting. It did no such thing, but as with previous such reports, this is how anti-vaping activists are likely to misrepresent this study.

On 2017 Jul 28, Miguel Lopez-Lazaro commented:

Cancer etiology: assumptions lead to erroneous conclusion

The authors claim that cancer is caused and driven by mutations, and that two-thirds of the mutations required for cancer are caused by unavoidable errors arising during DNA replication. The first claim is based on the somatic mutation theory. The second claim is based on a highly positive correlation between the lifetime number of stem cell divisions in a tissue and the risk of cancer in that tissue, and on their method for estimating the proportion of mutations that result from heredity (H mutations), environmental factors (E mutations) and unavoidable errors arising during DNA replication (R mutations). These claims raise several questions:

1. Sequencing studies have found zero mutations in the genes of a variable proportion of different cancer types (see, e.g., https://dx.doi.org/10.1093/jnci/dju405 and references therein). If cancer is caused by mutations in driver genes, could the authors explain what causes these cancers with zero mutations? Could the authors use their method for estimating the proportion of cancer risk that is preventable and unpreventable in people with tumors lacking driver gene mutations?

2. Environmental factors are known to affect stem cell division rates. According to IARC, drinking very hot beverages probably causes esophageal cancer (Group 2A). If you drink something hot enough to severely damage the cells lining the esophagus, the stem cells located in deeper layers have to divide to produce new cells to replace the damaged cells. These stem cell divisions, triggered by an environmental factor, will lead to mutations arising during DNA replication. However, these mutations are avoidable if you do not drink very hot beverages. Should these mutations be counted as environmental mutations (H mutations) or as unavoidable mutations arising during DNA replication (R mutations)?

3. The authors' work is based on the somatic mutation theory. This theory is primarily supported by the idea that cancer incidence increases exponentially with age. Since our cells are known to accumulate mutations throughout life, the accumulation of driver gene mutations in our cells would perfectly explain why the risk of cancer increases until death. However, it is now well established that cancer incidence does not increase exponentially with age for some cancers (acute lymphoblastic leukemia, testicular cancer, cervical cancer, Hodgkin lymphoma, thyroid cancer, bone cancer, etc). It is also well known that cancer incidence decreases late in life for many cancer types (lung cancer, breast cancer, prostate cancer, etc). For example, according to SEER cancer statistics review, 1975-2014, men in their 80s have approximately half the risk of developing prostate cancer than men in their 70s. The somatic mutation theory, which is the basis for this article, does not explain why the lifetime accumulation of driver gene mutations in the cells of many tissues is not translated into an increase in cancer incidence throughout life. Are the authors' conclusions applicable to all cancers or only to those few cancers in which incidence increases exponentially with age until death?

4. The authors estimate that 23% of the mutations required for the development of pancreatic cancer are associated with environmental and hereditary factors; the rest (77%) are mutations arising during DNA replication. However, Notta et al. recently found that 65.4% of pancreatic tumors develop catastrophic mitotic events that lead to mutations associated with massive genomic rearrangements (https://doi.org/10.1038/nature19823). In other words, Notta et al. demonstrate that cell division not only leads to mutations arising during DNA replication, but also to mutations arising during mitosis. For this cancer type, the authors could introduce a fourth source of mutations, and estimate the proportion of mutations arising during mitosis (M mutations) and re-estimate those arising during DNA replication (R mutations). Alternatively, they could reanalyze their raw data without assuming that the parameters “stem cell divisions” and ”DNA replication mutations” are interchangeable. Cell division, process by which a cell copies and separates its cellular components to finally split into two cells, can lead to mutations occurring during DNA replication, but also to other cancer-promoting errors, such as chromosome aberrations arising during mitosis, errors in the distribution of cell-fate determinants between the daughter cells, and failures to restore physical interactions with other tissue components. Would the authors' conclusions stand without assuming that the parameters “stem cell divisions” and ”DNA replication mutations” are interchangeable?

5. The authors report a striking correlation between the number of stem cell divisions in a tissue and the risk of cancer in that tissue. They do not report any correlation between the number of mutations in a tissue and the risk of cancer in that tissue; in fact, these parameters are not correlated (see. e.g., https://doi.org/10.1038/nature19768). In addition, the authors discuss that most of the mutations required for cancer are a consequence, not a cause, of the division of stem cells. So, why do the authors use their correlation to say that cancer is caused by the accumulation of mutations in driver genes instead of saying that cancer is caused by the accumulation of cell divisions in stem cells?

For references and additional information see: Comment on 'Stem cell divisions, somatic mutations, cancer etiology, and cancer prevention' DOI: 10.13140/RG.2.2.28889.21602 https://www.researchgate.net/publication/318744904; also https://www.preprints.org/manuscript/201707.0074/v1/download

On 2017 Mar 29, Daniel Corcos commented:

The authors confuse mutation incidence with cancer incidence. Furthermore the factors are not additive. Mutations are obviously related to the number of cell divisions, which is well known, but this does not tell anything on the contribution of heredity and environment.

On 2017 Mar 29, Atanas G. Atanasov commented:

Compliments to the authors for this so interesting work, I have featured it at: http://healthandscienceportal.blogspot.com/2017/03/new-study-points-that-two-thirds-of.html

On 2017 Apr 26, Zhang Weihua commented:

These authors should have cited our publication that, for the first time, shows that multinucleated giant cells are drug resistant and capable of generating tumors and metastases from a single cell in vivo.

Formation of solid tumors by a single multinucleated cancer cell. Weihua Z, Lin Q, Ramoth AJ, Fan D, Fidler IJ. Cancer. 2011 Sep 1;117(17):4092-9. doi: 10.1002/cncr.26021. Epub 2011 Mar 1. PMID: 21365635

On 2017 Aug 04, L Lefferts commented:

This study funded by members of the International Association of Color Manufacturers (IACM) and written by IACM staff, members, and consultants touting the safety of food dyes is so riddled with inaccuracies and misleading statements that it should be retracted and disregarded. Each of its conclusions is incorrect. The Corrigendum only partially and inadequately addresses the errors. Bastaki et al. mischaracterizes the relationship between the study’s exposure estimates and actual concentrations measured analytically by the US Food and Drug Administration (FDA), systematically underestimates food dye exposure, and relies on acceptable daily intake (ADI) estimates that are based on outdated animal studies that are incapable of detecting the kinds of adverse behavioral effects reported in multiple double-blind clinical trials in children. Bastaki ignores the nine recent reviews (including three meta-analyses) drawing from over 30 such double-blind clinical trials that all conclude that excluding food dyes, or adherence to a diet that eliminates food dyes as well as certain other foods and ingredients, reduces adverse behavior in some children (Arnold et al. 2012, Arnold et al. 2013, Faraone and Antshel 2014, Nigg et al. 2012, Nigg and Holton 2014, Schab and Trinh 2004, Sonuga-Barke et al. 2013, Stevens et al. 2011, Stevenson et al. 2014). While Bastaki et al. has been revised to delete the incorrectly reported doses used in the Southampton study, it makes misleading statements about the Southampton study.

Each erroneous conclusion is addressed in turn, in a letter sent to the editor, signed by myself, Lisa Lefferts, Senior Scientist, Center for Science in the Public Interest, and Jim Stevenson, Emeritus Professor of Developmental psychopathology, School of Psychology, University of Southampton, and available at <https://cspinet.org/sites/default/files/attachment/dyes Bastaki LTE.pdf>.

On 2017 Sep 23, Markus Meissner commented:

During this lengthy discussion, the Kursula group succeeded to solve part of the puzzle regarding the polymerisation mechanism of apicomplexan actin and confirmed our suspicions (see below) that sedimentation assays, while useful in other systems, lead to variable and unreliable results in case of apicomplexan actin (see: https://www.nature.com/articles/s41598-017-11330-w). Briefly, in this study polymerisation assays based on pyrene labelling were used to compare polymerisation kinetics of Plasmodium and rabbit actin and conclusively showed that: - Apicomplexan Actin polymerises in a cooperative manner with a similar critical concentration as canonical Actin - Shorter filament lengths result from higher depolymerisation rate. Since Skillmann et al., 2013 reached their conclusion exclusively based on sedimentation assays, their conclusion regarding an isodesmic polymerization mechanism of apicomplexan actin, as discussed below, should be seen with great scepticism. As discussed in this study these in vitro data also support our (Periz et al., 2017, Whitelaw et al., 2017 and Das et al., 2017) findings in vivo suggesting that a critical concentration of G-actin is required in order to form F-actin filaments. Therefore, the hypothesis of an isodesmic polymerisation mechanism can be considered as falsified.

On 2017 Jun 20, Robert Insall commented:

Professor Sibley's most extensive comments are based around a single paper (Skillman et al. 2013) that concluded the polymerization of Toxoplasma actin uses an isodesmic, rather than a nucleation-based mechanism. While this work was well-executed, and thorough, it is not on its own sufficient to support the level of absolutism that is in evidence in these comments. In particular, results from actin that has been exogenously expressed (in this case, in baculovirus) are less reliable than native apicomplexan actin. The folding of actin is infamously complex, with a full set of specialist chaperones and idiosyncratic N-terminal modifications. Even changes in the translation rate of native actin can affect its function and stability (see for example Zhang, 2010). Exogenously-expressed actin may be fully-folded, but still not representative of the physiological protein. Thus it is not yet appropriate to make dogmatic statements about the mechanism of apicomplexan actin function until native actin has been purified and its polymerization measured. When this occurs, as it surely will soon, stronger rulings may be appropriate.

On 2017 Jun 20, Markus Meissner commented:

We thank David Sibley for his last comment. As we mentioned previously, it was not the aim of this study to prove or disprove isodesmic polymerisation. We highlighted the current discussion in the field regarding isodesmic polymerisation (see previous comments). It is contra productive to turn the comments on this paper into a discussion on Skillmann et al., 2013, which is seen with great scepticism in the field. We made our views clear in previous responses and we hope that future results will help to clarify this issue. However, we find it concerning (and distracting) that– in contrast to his earlier comments, according to which our data can be consolidated with isodesmic polymerisation -David Sibley is now doubting the validity of our data, mentioning that CB might affect actin dynamics. This is certainly the case, as shown in the study and as is the case with most actin binding proteins used to measure actin dynamics in eukaryotic cells. This issue was discussed at length in the manuscript, by the reviewers comments and authors response, which can all be easily accessed: https://elifesciences.org/articles/24119 The above statement reflect the joint opinions of: Markus Meissner (University of Glasgow), Aoife Heaslip (University of Conneticut) and Robert Insall (Beatson Institute, Glasgow).

On 2017 Jun 19, L David Sibley commented:

Based on the most recent response by Dr. Meissner, it is clear that there is still some confusion about the difference between measuring the kinetics of actin polymerization in vivo vs. monitoring actin dynamics in vivo. These are fundamentally different processes, the former of which cannot be directly inferred from the later. Given this confusion, it is worth reviewing how these two processes are distinct, yet inter-related.

When referring to the mechanism of actin polymerization in vitro, nucleation is the process of forming stable trimers, which are normally limited by an intrinsic kinetic barrier imposed by unstable dimers. Due to this intrinsic instability, the nucleation step is normally revealed as a pronounced lag phase in the time course of polymerization, after which filaments undergo rapid elongation Pollard TD, 2000. TgACT1 lacks this nucleation step and instead uses a non-cooperative, isodesmic process. The Arp/23 complex facilitates formation of the trimer by acting as the barbed end, thus reducing the lag time and accelerating polymerization, typically by side branching from existing filaments. Toxoplasma has no use for such a step as it would not affect the efficiency of an isodesmic process since dimers and trimers normally form without a lag phase Skillman KM, 2011. By contrast, formins bind to barbed end of existing filaments and promote elongation, both by preventing capping protein from binding and by using profilin to gather actin monomers for addition to the barbed end. Formins may also nucleate F-actin by binding to two monomers to lower the lag phase for trimer formation, thus facilitating elongation, although this role is less well studied. Importantly, formins can act on actins that use either an intrinsic “nucleation-elongation” cooperative mechanism or an isodesmic process, such as that used by Toxoplasma. Hence, the fact that formins function in Toxoplasma has no bearing on the intrinsic polymerization mechanism of TgACT1.

Once the above definitions are clearly understood, it becomes apparent why the isodesmic process of actin nucleation used by Toxoplasma is fully compatible with both the short filament, rapid turnover dynamics that have been described previously Sahoo N, 2006, Skillman KM, 2011, Wetzel DM, 2003, and the new findings of long-stable filaments described in the present paper Periz J, 2017. These different states of actin polymerization represent dynamics that are driven by the combination of the intrinsic polymerization mechanism and various actin-binding proteins that modulate this process. However, the dynamic processes that affect the status of G and F-actin in vivo cannot be used to infer anything about the intrinsic mechanism of actin polymerization as it occurs in solution. As such, we strongly disagree that there is an issue to resolve regarding the intrinsic mechanism of actin polymerization in Toxoplasma nor do any of the studies in the present report address this point. Our data on the in vitro polymerization kinetics of TgACT1 clearly fit an isodesmic process Skillman KM, 2013 and we are unaware of any data that demonstrates otherwise. Hence we fail to see why this conclusion is controversial and find it surprising that these authors continue to question this point in their present work Periz J, 2017, previous report Whitelaw JA, 2017, and comments by Dr. Meissner. As it is not possible to predict the intrinsic mechanism of actin polymerization from the behavior observed in vivo, these comments are erroneous and misleading. On the other hand, if these authors have new data that speaks directly to the topic of the intrinsic polymerization mechanism of TgACT1, we would welcome them to provide it for discussion.

Although we disagree with the authors on the above points, we do agree that the fact that actin filaments can be visualized in Toxoplasma for the first time is interesting and certainly in contrast to previous studies. For example, previous studies failed to reveal such filaments using YFP-ACT1, despite the fact that this tagged form of actin is readily incorporated into Jasplakinolide-stabilized filaments Rosenberg P, 1989. As well, filaments have not been seen by CryoEM tomography Paredes-Santos TC, 2012 or by many studies using conventional transmission EM. This raises some concern that the use of chromobodies (Cb) that react to F-actin may stabilize filaments and thus affect dynamics. Although the authors make some attempt to monitor this in transfected cells, it is very difficult rule out that Cb are in fact enhancing filament formation. One example of this is seen in Figure 6 A, where in a transiently transfect cell, actin filaments are seen with both the Cb-staining and anti-actin, while in the non-transfected cell, it is much less clear that filaments are detected with anti-actin Periz J, 2017. Instead the pattern looks more like punctate clusters that concentrate at the posterior pole or residual body. Thus while we would agree that the Cb-stained filaments also stain with antibodies ot F-actin, it is much less clear that they exist in the absence of Cb expression. It would thus be nice to see these findings independently reproduced with another technique. It would also be appropriate to test the influence of Cb on TgACT1 in vitro to determine if it stabilizes filaments. There are published methods to express Toxoplasma actin in a functional state and so this could easily be tested Skillman KM, 2013. Given the isodesmic mechanism used by TgACT1, it is very likely that any F-actin binding protein would increase the stability of the short filaments that normally form spontaneously, thus leading to longer, more stable filaments. This effect is likely to be less pronounced when using yeast or mammalian actins as they intrinsically form stable filaments above their critical concentration. Testing the effects of Cb on TgACT1 polymerization in vitro would provide a much more sensitive readout than has been provided here, and would help address the question of whether expression of Cb alters in vivo actin dynamics.

In summary, we find the reported findings of interest, but do not agree that they change the view of how actin polymerization operates in Toxoplasma at the level of the intrinsic mechanism. They instead reveal an important aspect of in vivo dynamics and it will be import to determine what factors regulate this process in future studies.

The above statement reflect the joint opinions of: John Cooper (Washington University), Dave Sept (University of Michigan) and David Sibley (Washington University).

On 2017 Jun 16, Markus Meissner commented:

Thank you for your comment which appears to be only a slight update of the comments already made on the eLIFE website and it would be helpful for all readers who wish to follow this discussion if we could stick to the website where the discussion started (see: https://elifesciences.org/articles/24119).

Regarding the second comment of David Sibley: It is good to see that the authors of the Skillmann paper (Skilmann et al., 2013) are able to reconcile our data with their unusual, isodesmic polymerisation model, despite their initial interpretations that clearly states that “…an isodesmic mechanism results in a distribution of SMALL OLIGOMERS, which explains why TgACTI only sediments efficiently at higher g force. Our findings also explain why long TgACTI filaments have not been observed in parasites by any method, including EM, fluorescence imaging of GFP–TgACTI and Ph staining." While it appears that we will need a lengthy discussion about Skillmann et al., 2013 or even better more reliable assays to answer the question of isodesmic vs cooperative polymerisation, our study did not aim to answer this open issue that we briefly introduced in Periz et al., 2017 to give a more complete picture of the open questions regarding apicomplexan actin. As soon as more convincing evidences are available for cooperative or isodesmic polymerisation of apicomplexan actin, we will be happy to integrate it in our interpretation. Meanwhile we remain of the opinion that our in vivo data (see also Whitelaw et al., 2017) best reflects the known behaviours of canonical actin. While it seems that under the conditions used by Skillmann et al., 2013 apicomplexan actin polymerizes in an isodemic manner, in the in vivo situation F-actin behaviour appears very similar to other, well characterised model systems. However, we would like to point out that a major argument in the interpretation of Skillmann et al., 2013 for isodesmic polymerisation is that “This discovery explains previous differences from conventional actins and offers insight into the behaviour of the parasite in vivo. First, nucleation is not rate limiting, so that T.gondii does not need nucleation-promoting factors. Indeed, homologs of actin nucleating proteins, such as Arp2/3 complex have not been identified within apicomplexan genomes”. This statement is oversimplified and cannot be reconciled with the literature on eukaryotic actin. For example, Arp2/3 knockouts have been produced in various cell lines (and obviously their actin doesn’t switch to an isodesmic polymerisation process). Instead, within cells, regulated actin assembly is initiated by two major classes of actin nucleators, the Arp2/3 complex and the formins (Butler and Cooper, 2012). Therefore, we thought it is necessary to mention in Periz et al., 2017 that apicomplexans do possess nucleators, such as formins. Several studies agree, that apicomplexan formins efficiently NUCLEATE actin in vitro, both rabbit and apicomplexan actin (Skillmann et al., 2012, Daher et al., 2010 and Baum et al., 2008). In summary we agree that future experiments will be required to solve this issue and we are glad that David Sibley agrees with the primary findings of our study. We hope that future in vitro studies will help to solve the question of isodesmic vs cooperative polymerisation mechanism in the case of apicomplexan actin so that a better integration of in vivo and in vitro data will be possible.

On 2017 Jun 14, L David Sibley commented:

We feel it is worth briefly reviewing the concept of the critical concentration (Cc), and the properties of nucleation-dependent actin polymerization, since there seems to be some misconception about these terms as they are used in this paper Periz J, 2017.

Polymerization assays using muscle or yeast actin clearly show that these actins undergo nucleation dependent assembly. Nucleation is a cooperative assembly process in which monomers of actin (i.e. G-actin) form small, unstable oligomers that readily dissociate. The Cc is the concentration of free actin above which a stable nucleus is formed and the filament elongation begins, a process that is more thermodynamically favorable than the nucleation step. A key feature of this nucleation-elongation mechanism is that for total actin concentrations above the Cc, the concentration of free G-actin remains fixed at the Cc, and all of the additional actin, over and above the Cc, is polymerized into filaments (i.e. F-actin). In contrast, an isodesmic polymerization process is not cooperative, and all steps (formation of dimer, trimer, etc.,) occur with the same binding and rate constants. With isodesmic polymerization, the monomer concentration (G-actin concentration) does not display a fixed limit; instead, as total actin concentration increased, the G-actin concentration continues to increase. Another key difference with isodesmic polymerization is that polymer forms at all concentrations of total actin (i.e. there is no concept of a critical concentration, Cc, that must be exceeded in order to achieve polymer formation).

The inherent differences between nucleation-elongation and isodesmic polymerization give rise to distinct kinetic and thermodynamic signatures in experiments. Because the nucleation process is unfavorable and cooperative, the time course of nucleation-elongation polymerization shows a characteristic lag phase, with a relatively low rate of initial growth, before the favorable elongation phase occurs. In contrast, isodesmic polymerization shows no lag phase, but exhibits linear growth vs. time from the start at time zero. The thermodynamic differences are manifested in experiments examining the fractions of polymer (F-actin) and monomer (G-actin) at steady state. Since nucleation-elongation has a critical concentration (Cc), the monomer concentration plateaus at this value and remains flat as the total protein concentration is increased. Polymer concentration is zero until the total concentration exceeds the critical concentration, and above that point, all the additional protein exists as polymer. In the isodesmic model, in stark contrast, the monomer concentration continues to increase and polymer form at all concentrations of total protein. These two distinct behaviors are illustrated in Figure 1 from Miraldi ER, 2008.

Our previous study on yeast and Toxoplasma actin Skillman KM, 2013 shows sedimentation assays that are closely matched by the theoretical results discussed above. In our study yeast actin (ScACT, Figure 2c) displays the saturation behavior characteristic of a nucleation-elongation mechanism; however, for TgACT1 (Figure 2a), the monomer concentration (red) continues to increase as total actin increases. In addition, the inset to Figure 2a shows that filaments (blue) are present at the lowest concentrations of total actin, and also does not exhibit a lag Skillman KM, 2013. Based on these features, it is unequivocal that Toxoplasma actin follows an isodemic polymerization process, with no evidence of cooperativity.

Several of the comments in the response may lead the reader to confound polymerization behavior in vitro with that observed fro actin polymerization in vivo in cells. The question of whether actin polymerization occurs by a nucleation-elongation mechanism or by an isodesmic mechanism is one that can only be determined in vitro using a solution of pure actin, because this is a property of the actin molecule itself, irrespective of other components. While the in vitro polymerization behavior is relevant as the template upon which various actin-binding proteins act, the polymerization mechanism for the actin alone cannot be inferred from in vivo observations due to the presence of actin-interacting proteins.

The authors state that the presence of “nucleation centers” in the parasite is not easy to consolidate with the isodesmic model Periz J, 2017. We disagree completely and emphatically. We agree that there are “centers” of accumulation of F-actin in the cell, these foci should not be referred to as “nucleation” centers in this case, because the term “nucleation” has a specific meaning in regard to the polymerization mechanism. F-actin may accumulate in these foci over time as a result of any one or more of several dynamic processes – new filament formation, elongation of short filaments, decreased turnover, or clustering of pre-existing filaments. The result is interesting and important; however, the result cannot be used to infer a polymerization mechanism.

The authors imply that these centers of F-actin correspond with sites of action of formins Periz J, 2017, which are capable of binding to actin monomers or actin filaments and thereby promoting actin polymerization. With vertebrate or yeast actin, which has a nucleation-elongation mechanism, formins do accelerate the nucleation process, and they also promote the elongation process. In the case of the isodesmic model for actin polymerization, formins would still function to promote polymerization, by interacting with actin filaments and actin monomers. Indeed, the short filaments that formed with the isodesmic mechanism are ideal templates for elongation from the barbed end (which formins enhance). We have previously shown that when TgACT1 polymerized in the presence of formins assembles into clusters of intermediate sized filaments that resemble the in vivo centers Skillman KM, 2012. Hence, as we commented previously, the isodesmic mechanism is entirely consistent with the observed in vivo structures labeled by the chromobodies.

The authors also suggest that evidence of a nucleation-elongation mechanism, with a critical concentration, is provided by the observation that actin filaments seen by chromobodies in vivo do not form in a conditional knock down of TgACT1 Periz J, 2017. In our view, this conclusion is based on incorrectly using observations of in vivo dynamics to infer the intrinsic polymerization mechanism of pure actin protein. Higher total actin concentration leads to higher actin filament concentration under both models, with control provided by the various actin-binding proteins of the cell and their relative ability to drive filament formation and turnover in vivo. However, dependence on total actin concentration is not a reflection of the intrinsic polymerization mechanism. The polymerization mechanism of TgACT1, whether isodesmic or nucleation-elongation, is unlikely to be the critical determinant of actin dynamics in vitro; instead, actin monomers and filaments are substrates for numerous actin-binding proteins that regulation filament elongation, filament turnover, and G-actin sequestration, that is, the whole of actin cytoskeleton dynamics.

Although we agree that much more study is need to unlock the molecular basis of actin polymerization and dynamics in apicomplexans, it will be important to distinguish between properties that are intrinsic to the polymerization process as it occurs in vitro, vs. interactions with proteins that modulate actin dynamics in vivo. The challenge, as has been the case in better studied systems Pollard TD, 2000, will be to integrate both sets of findings into a cohesive model of actin regulation and function in apicomplexans.

The above statement reflect the joint opinions of: John Cooper (Washington University), Dave Sept (University of Michigan) and David Sibley (Washington University).

On 2017 Apr 05, thomas samaras commented:

This study supports the work of Lindeberg and Lundh some 25 years ago. They found no evidence of CHD or stroke among the natives of Kitava. They also reported no evidence of CHD and stroke in all of Papua New Guinea. Eaton et al, also reported the rarity or absence of CHD and stroke in the Solomon Islands, PNG, Kalahari bushmen, and Congo pygmies.

Lindeberg and Lundh, Apparent absence of stroke and ischaemic heart disease in a traditional Melanesian island: a clinical study in Kitava, Journal of Internal Medicine 1993; 233: 269-275.

Eaton, Konner, Sostak, Stone agers in the fast lane: chronic degenerative diseases in evolutionary perspective. The American Journal of Medicine, 1988; 84;, 739-749

On 2017 Jun 02, Nicholas J L Brown commented:

This article has been retracted: http://onlinelibrary.wiley.com/doi/10.1111/apt.14044/full

On 2017 Mar 27, Janet Kern commented:

In the Endres et al. study above, they found a marginally significant trend in decreased glutathione (GSH) signals between the two groups in the dorsolateral prefrontal cortex (p=0.076). It did not quite reach statistical significance. To achieve statistical significance, a study must have sufficient statistical power. Statistical power, or the power of a test to correctly reject the null hypothesis, is affected by the effect size, sample size, alpha significance criterion. In their study, the overall and single-group differences in neurometabolite signals, the level of significance was corrected for multiple tests using the Bonferroni approach (p < 0.025 due to performing the measurements in two independent regions). So, the alpha significance criterion was 0.025. Effect size is the magnitude of the sizes of associations or the sizes of differences. Typically, a small effect size is considered about 0.2; a medium effect size is considered about 0.5; and a large effect size is considered about 0.8. Assuming an alpha, two tailed, set at 0.025, and a large effect size of 0.8 and a power of 0.8, the total number of subjects required would need to be 62 (or 31 in each group). The sample size the Endres et al. study was 24 ASD patients and 18 matched control subjects. Was there truly no statistically significant difference between the two groups, or was the study underpowered?

On 2017 Dec 03, Philippe Katz commented:

Very interesting article, will try your treatment.

On 2017 Sep 07, Noel de Miranda commented:

Interesting report that confirms the works of Kloor et al. 2005 Cancer Res and Dierssen et al. 2007 BMC Cancer which are not cited in the current work.

On 2017 Apr 22, Vojtech Huser commented:

This is a nice example of semantic integration. Inclusion of these CDEs in the common NIH portal for CDEs would be an added bonus.

On 2017 May 10, Helge Knüttel commented:

Unfortunately, the search strategy for this systematic review was not published by the journal. It may be found here.

On 2017 Mar 20, Atanas G. Atanasov commented:

Very good overview on MSM, I have featured this manuscript at: http://healthandscienceportal.blogspot.com/2017/03/the-novel-dietary-supplement.html

On 2017 Jun 04, Steve Alexander commented:

The title describes plasma, as does the findings. But the methods talks about serum, although it describes EDTA collection. I'm assuming it's plasma throughout, but it is confusing.

On 2017 Mar 22, Paola Pizzo commented:

We thank the Authors for their Reply to our Letter. However, given the importance of this topic, we have to add an additional comment to further clarify some criticisms. First, the Authors reason that the average mitochondrial surface in contact with ER can be extracted from the data presented in table S1, S2, S3 of their paper (Naon D, 2016). However, these data have not the same relevance that presenting the total number of ER-mitochondria contacts in the two situations. Indeed, the percentage of mitochondrial surface in contact with ER substantially varies whenever the analysis is restricted only to mitochondria that display contacts with the ER, or includes also contact-deprived mitochondria. In their analysis, the Authors considered only those mitochondria that are engaged in the interaction with the ER (and not the total mitochondrial population), as they stated in the Results section (“we devised an ER-mitochondria contact coefficient (ERMICC) that computes [....] the perimeter of the mitochondria involved in the interaction”). This approach could be misleading: considering that in Mfn2-depleted cells a higher percentage of mitochondria endowed with contacts has been found (Filadi R, 2016), the fraction of contact-deprived mitochondria should be taken into account to calculate the real average OMM juxtaposition surface. Second, the Authors argue that the fluorescent organelle proximity probes they used (both ddGFP and FRET-based FEMP probe) do not artificially juxtapose organelles: we did not claim this in our Letter, and we apologize if, for space limitations, this was not clear enough. Nevertheless, as to the FEMP probe, its propensity to artificially force ER-mitochondria juxtaposition, already after few minutes from rapamycin treatment, has been clearly shown by EM analysis in the original paper describing this tool (Csordás G, 2010). Additionally, it is worth to mention that comparison of FRET values between different conditions is possible only when the dynamic range (i.e., the difference between minimal and maximal FRET values) of a given FRET probe is similar in these different conditions. The new data provided by the Authors in their Reply (Tables 1 and 2) show that the average rapamycin-induced FRETmaximal values are dramatically different between wt and Mfn2-depleted cells. Thus, we believe that at least some cautions should be adopted to claim the use of this probe as a reliable tool for the comparison of ER-mitochondria tethering in such different conditions. Recently, we suggested how the fragmented/altered mitochondrial and ER morphology, present in Mfn2-depleted cells, may impair the rapamycin-induced assembly of this probe (Filadi R, 2017), thus severely complicating the interpretation of any result. Regarding the other fluorescent probe (the ddGFP) used by Naon et al. (Naon D, 2016), it is unclear why only ~10 % of the transfected wt/control cells (mt-RFP positive cells; Fig. 1G and 2E) are positive for the ddGFP signal (claimed as organelles tethering indicator). Should not ER-mitochondria juxtaposition be a feature of every cell? Concerning the Ca²⁺ experiments, we are forced to discuss additional criticisms present in the Authors’ Reply. Our observation that, in Naon et al. (Naon D, 2016), mitochondrial Ca²⁺ peaks in control cells (mt-YFP traces), presented in Fig. 3F, are ~ 100-fold higher than those in Fig. 3B was rejected by the Authors, because in Fig. 3F “Mfn2^flx/flx cells were preincubated in Ca²⁺ -free media to equalize cytosolic Ca²⁺ peaks”. However, in our Letter, we clearly referred to control, mt-YFP expressing cells, and not to Cre-infected Mfn2^flx/flx cells. Nevertheless, even if a “preincubation in a Ca²⁺ -free media to equalize cytosolic Ca²⁺ peaks” (i.e., a treatment that decreases the ER Ca²⁺ content) was applied to both cell types, the prediction is that, in Fig. 3F, the ATP-induced mitochondrial Ca²⁺ peaks would be lower for both Mfn2^flx/flx and control (mt-YFP) cells, and not higher than those presented in Fig. 3B. Lastly, as members of a lab where mitochondrial Ca²⁺ homeostasis has been studied over the last three decades, we have here to point out that, in our opinion, the reported values for ATP-induced mitochondrial [Ca²⁺ ] peaks (i.e., 160 nM and 390 nM in Fig. 3B and 3C, respectively) are unusually very low and hardly considerable to be over the basal mitochondrial matrix [Ca²⁺ ] (~ 100 nM). Furthermore, these low [Ca²⁺ ] values cannot be reliably measured by the mitochondrial aequorin probe (Brini M, 2008) used by Naon et al. (Naon D, 2016). Finally, concerning the speed of Ca²⁺ accumulation in isolated mitochondria, we clearly stated in our Letter that at 50 uM CaCl2 in the medium and no Mg^2+, the rate of Ca²⁺ accumulation is limited by the activity of the respiratory chain (Heaton GM, 1976), and thus does not offer any information on the MCU content. We did not refer to problems in respiratory chain activity in Mfn2-depleted cells, as interpreted by Naon et al. in their Reply.<br> Overall, while we appreciate the attempt of the Authors to highlight some aspects of the controversy, we renew all the concerns we discussed in our Letter.

On 2017 Apr 19, Martine Crasnier-Mednansky commented:

The authors have previously reported that very little SgrT is made in E. coli as compared to Salmonella typhimurium, which led them to conclude that E. coli K12 has "lost the need for SgrT" (Wadler CS, 2009). Later on, the rationale for using S. typhimurium instead of E. coli for studying SgrT was reinforced (Balasubramanian D, 2013). In the present work, the authors use E. coli sgrS mutant strains overproducing SgrT. Therefore, the present work does not establish a 'physiological' role for SgrT in preventing the E. coli PTS-transport of glucose, thus the title of the article is misleading.

The authors’ interpretation of figure 1 does not agree with the following data. E. coli mutant strains lacking Enzyme IICB^Glc (PtsG) do grow on glucose (see Curtis SJ, 1975; Table VIII in Stock JB, 1982). Mutant strains lacking both the glucose and mannose enzyme II grow very slowly on glucose. In other words, because growth had been observed on mannose, growth should have been observed on glucose. Furthermore, the authors should have been aware that an increased level of cAMP from overexpressing SgrT further impairs growth on glucose.

PtsG is not "comprised of three main functional domains", as the authors state. PtsG has two functional domains (IIB and IIC) connected by a flexible linker. In the nomenclature for PTS proteins (Saier MH Jr, 1992), PtsG translates into Enzyme IICB^Glc, which is informative (and therefore should be preferred to any other designations) because it indicates a two-domain structure, a specificity for glucose, and the order of the domains (from N to C terminus).

Kosfeld A, 2012 clearly established, by cross-linking experiments, the interaction between SgrT and Enzyme IICB^Glc in the presence of glucose. They also visualized the recruitment of SgrT to the membrane by in vivo fluorescence microscopy. It is therefore unwarranted for the authors to 'hypothesize' an interaction and localization to the membrane, and to state: "Once we established that SgrT inhibits PtsG specifically and its localization to the membrane …". In addition, the demonstration by Kosfeld A, 2012, the motif KTPGRED (in the flexible linker) is the main target for SgrT, is rather convincing.

Finally, the statement "SgrT-mediated relief of inducer exclusion may allow cells experiencing glucose-phosphate stress to utilize alternative carbon sources" is inaccurate because it ignores the positive effect of cAMP on the utilization of alternative carbon sources like lactose.

On 2017 May 28, Thomas Perls, MD, MPH commented:

Some studies cite this very compelling study as evidence against the Compression of Morbidity hypothesis. This study observes progressively higher prevalence rates of morbidity and disability with increasing age among octogenarians, nonagenarians and centenarians. However, they were unable to determine when in their lives these individuals developed these problems and therefore the work does not describe any differences in compression of disability of morbidity. One of the virtues of becoming a centenarian is the likelihood of compressing the time that you experience disability towards the end of your life. Surviving to ages that relatively approach human lifespan (e.g. >105 years) likely also entails compressing morbidity as well Andersen SL, 2012.

On 2017 Mar 19, Mauro Podda commented:

Dear Sir/Madam. Many thanks for showing your interest in our manuscript. We can guarantee that our systematic review with meta-analysis of RCTs comparing antibiotic therapy and surgery for uncomplicated acute appendicitis has been performed accordingly with the instructions provided by the Cochrane handbook for systematic review of interventions, and the PRISMA statement has been used for reporting research in the systematic review. Probably, this should better clarified in the text. With regards to the search keys, this is the strategy: (((((appendicitis) AND antibiotic treatment) OR conservative management) OR nonoperative management) OR nonoperative treatment) AND appendectomy

On 2017 Mar 16, Michelle Fiander commented:

What is a Systematic Literature Search?

This review describes its literature search as "systematic" but provides no evidence to support the statement. Reproducible search strategies are not provided--per PRISMA 8, but two sets of keywords are. I created a PubMed search strategy (copied below) by making an educated guess as to how the authors combined the list of terms provided and in doing so, found over 3800 citations up to April 2016 (one month before the search date reported in the review). The review reports screening 938 citations so it is unclear how the evidence for this review were identified.

The authors say the meta-analysis was "performed in accordance with the recommendations from the...PRISMA Statement." PRISMA does not recommend methodological approaches to data analysis, it describes the data authors should provide in a systematic review manuscript. For recommendations on how to analyze data in a systematic review, sources such as The Cochrane Handbook should be consulted.

There has been recent research on the poor quality of published systematic reviews; journal editors should engage with methodologists conversant with systematic review methodology to ensure the reviews it publishes are rigorously reported.

PubMed: Search (antibiotic OR "nonoperative treatment" OR "conservative management" OR "nonoperative management" OR "medical treatment" OR appendectomy OR appendicectomy OR laparoscopy) AND ("acute appendicitis") AND Filters: Publication date to 2016/04/30

On 2017 Apr 23, Wenqiang Yu commented:

My comments on this impressive paper are mainly regarding the relationship between the enhancer and microRNA. MicroRNAs are expressed in a tissue and cell type specific manner, as is the enhancer. Therefore, it would be intriguing to know whether miRNA and enhancer may be intrinsically linked while regulating gene expression. Results of this paper are interesting because Suzuki HI et al found that enhancer regions overlap with miRNA genome loci and may play a role in shaping the tissue-specific gene expression pattern. These findings directly support our earlier results from a 5-year long project that was finally published in RNA biology in the beginning of 2016, “MicroRNAs Activate Gene Transcription Epigenetically as an Enhancer Trigger”.(http://www.tandfonline.com/doi/abs/10.1080/15476286.2015.1112487?journalCode=krnb20) In this paper, we not only found that many miRNA genome loci overlap with enhancer regions, but also identified a subset of miRNAs in the nucleus that function as universal and natural gene activators emanating from the enhancer loci, which we termed NamiRNA (Nuclear activating miRNA; although this specific term was not used in the paper). These miRNAs are associated with active enhancers characterized by distinct H3K27ac enrichment, p300/CBP binding and DNase I hypersensitivity. We also presented evidence that NamiRNA promotes genome-wide gene transcription through the binding and activating of its targeted enhancers. Thus, we anticipate that NamiRNA-enhancer-mRNA activation network may be involved in cell behavior modulation during development and disease progression. Having said all that, we hope our results published in RNA biology can be cited by this paper. Meanwhile, we want to emphasize the dual functionality of miRNAs that is supported by our results---work as an activator via enhancer in the nucleus and as a traditional silencer in the cytoplasm. In light of this, more attention should be paid towards research that clarifies the detail of these NamiRNAs functions. It is in our belief that the miRNA-enhancer-gene activation network may be the intrinsic link between miRNA and enhancer when the two coordinate in regulating gene expression during cell fate transitions.

On 2017 May 04, Ralph Brinks commented:

One of the key methods used in this paper is not appropriate. Note the comment on this paper: Hoyer A, 2017

On 2017 Mar 11, Lydia Maniatis commented:

Reading this article, one gets the impression that the authors don’t quite believe their own claims, or aren’t really sure about what they’re claiming. This is illustrated by the following statement (caps mine): “It could be that other factors often associated with perceptual inferences and top-down processing—scission, grouping, object formation, and so forth—could affect the filters OR ACTUALLY ARE THE FILTERS” (page 17).

Whereas up to this point the notion of “filters,” described as acting “early” in the visual process, has referred to a technical manipulation of the image based on sharpening or blurring luminance “edges” (a process which is unnecessarily and somewhat confusingly described in terms of removing “low or high spatial frequency content,” even though the elements referred to are not repeating) we are now told that this manipulation - the “simple filter” - may be equivalent to processes of perceptual organization that produce de facto inferences about the distal stimulus, such as the process of figure-ground segregation (which is, of course, prior to “object formation”). This is quite a surprise – in this case we perhaps could refer to, and more explicitly address, these organizing processes - assuming the authors decide definitively that this is what they mean, or unless the term “filter” is only intended to mean “whatever processes are responsible for certain products of perception.”

With respect to the specific story being told: As with all "spatial filtering" accounts to date, it is acknowledged to be ad hoc, and to apply to a small, arbitrary set of cases (those for which it has been found to "work"). Which means that it is falsified by those cases which it cannot explain. The ad hoc-ness is incorporated into the “hypothesis: “The results support the hypothesis that, under some conditions, high spatial frequency content remains invariant to changes in illuminant” (p. 17). Which conditions are being referred to is not specified, begging the question of the underlying rationale. The authors continue to say that “Of course, this hypothesis may not be true for complex scenes with multiple illuminants or large amounts of interreflection.” Arguably, all natural scenes are effectively under multiple illuminants due to shadows created by obstructions and orientations relative to light sources.

In fact, as with all filtering accounts to date, the account doesn’t even adequately explain the cases it is supposed to explain. The reason for this is that it doesn’t address the “double layers” present in perception with respect to illumination. It isn't fair to say that when a perceived surface is covered by a perceived shadow, we are discarding the illumination; the shadow is part of the percept. So to the extent that Dixon and Shapiro’s manipulation describes the perceptual product as containing only perceived surface lightness/color values but not illumination values, it is not representative of the percept corresponding to the image being manipulated.

Relatedly, Dixon and Shapiro don’t seem to understand the nature of the problem they are addressing. They say that: “Most explanations of the dress assume that a central task of color perception is to infer the reflectance of surface material by way of discounting the illumination falling on the object” (p. 14). This may be accurate with respect to “most explanations” but, again, such explanations are inapt. As I have noted in connection to one such explanation (https://pubpeer.com/publications/17A22CF96405DA0181E677D42CC49E), attributing perceived surface color to perceived illumination is equivalent to attributing perceived illumination color/quality to perceived surface color. They are simultaneous and correlated inferences, and treating one as a cause of the other is like treating the height of one side of a seesaw as the cause of the height of the other side. You need to explain both what you see and what you saw.

The confusion is similarly illustrated in Dixon and Shapiro's description of Purves’ cube demo, described as “an iconic image for illustrating the effect of illumination on color appearance…” (p. 3). But the demo is actually not illuminated if on a computer screen, and if observed on a page, is typically observed under ordinary lighting. Again, both the color of the surfaces and the color of the illumination are inferred on the basis of the chromatic structure of the unitary image (of its retinal projection); and both are effects, not causes, and both are represented in perception. I see the fabric of the dress as white and gold, and the illumination as bluish shadow. Neither is “discounted” in the sense that Dixon and Shapiro seem to be claiming.

With respect to the problem of the dress specifically, none of these explanations address why it interpreted one way by some, another way by others. The ambiguity of light/surface applies to all images, so general explanations in terms of illumination/surface color estimation don't differentiate cases in which there is agreement from those rarer ones for which there is disagreement. The reference to one perceptual outcome of the dress as indicating “poor color constancy” or “good color constancy” is inapt as the images do not differ in illumination, or surface color, but only in interpretation.

As I've also noted previously, the proof of understanding the dress is to be able to construct other images with similar properties. So far they've only been found by chance.

On 2017 Nov 29, Natalie Clairoux commented:

Free version of this article available after December 31, 2018 at https://papyrus.bib.umontreal.ca/xmlui/handle/1866/19671

On 2017 Apr 18, Seán Turner commented:

The genus name Eggerthella is not novel: Eggerthella Wade et al. 1999 (PubMed Id 10319481). In the title, "gen. nov." should be replaced by "sp. nov."

On 2017 Apr 18, Seán Turner commented:

The authors refer to the type strain variably as "Marseille P-3114", "Marseille-P3114", and "Marseille-P-3114" in the manuscript. Both "Marseille-P3114" and "Marseille-P-3114" are used in the protologue of the novel species Metaprevotella massiliensis.

On 2017 Apr 17, Seán Turner commented:

Contrary to the title, Pseudoflavonifractor is not a novel genus (Pseudoflavonifractor Carlier et al. 2010; PubMed Id 19654357).

On 2017 Mar 10, Melissa Vaught commented:

Prior randomized controlled trials have examined the impact of organizational social media promotion (i.e., using journal’s official social media accounts) on article views (Fox CS, 2015, Fox CS, 2016, Adams CE, 2016) or on article downloads and citations (Tonia T, 2016). With the exception of Adams CE, 2016, no significant effect of social media posting on page views or downloads has been observed. However, a key question has remained: Might sharing by individuals have an effect where publisher promotion has not?

The trial reported here attempts to address this question directly. The authors enlisted members and trainees on its editorial board to share links to articles from their personal social media accounts (enhanced Twitter intervention). Outcomes were compared to control and to sharing via the journal’s official Twitter account (basic Twitter intervention). Selected publications were between 2 months and more than 2 years old at the time of intervention.

Similar to Fox CS, 2015, Fox CS, 2016, & Tonia T, 2016, posts by the @JACRJournal account did not increase article views (though removing a ‘most read’ outlier that had been randomized to the control group changed this conclusion). As summarized in the abstract, weekly page views were higher in the enhanced intervention than in control and basic groups. In fact, the enhanced group outperformed the basic group in all 4 primary and secondary endpoints. Authors found no significant effect of publication age.

The authors note that the difference between enhanced and basic groups may derive from multiple vs. single posting of a link. The difference in effects is not proportional to the number of posts, and as the authors note, Fox CS, 2016 used a high frequency social media posting to no avail. In addition, the JACR authors observed that 1 team had a much larger effect on page views than the other 3, and the effect did not track with follower count.

I would first note that some limitations in the methods and/or reporting might influence interpretation of these comparisons. Methods state that team members were assigned 1 article to tweet per day, and they were to only post about each article once. However, there is no indication that participants’ accounts were reviewed to check adherence to the instructions, in particular whether all 4 team members posted the assigned article with a functioning link on the designated day. It was unclear to me whether team members were sent a link the day they were assigned to post it, or whether these might have been provided in batches with instruction to tweet on the assigned day. The article also does not discuss how teams were assigned and whether members knew who their teammates were. Finally, although the team effect did not correlate with follower number, it would have been useful to know the number of followers for @JACRJournal at the start of the intervention, for comparison.

Nonetheless, the outsized effect on outcomes for 1 team is interesting. Though largely beyond the scope of this article, additional analytics could provide the basis for some interesting exploratory analysis and might be worth consideration in future studies of this type. At the Twitter account level, the authors reported the number of followers for each team member, but the age and general activity of the account during the intervention period could be relevant. Follower overlap between team members (or more refined user network analysis, as suggested by the authors) might also be informative.

It also might have been useful to also gather tweet-level analytics from team members, to identify high-engagement tweets (e.g., based on URL clicks and/or replies). This could determine whether team performance was driven by a single member, particular publications/topics, or discussion about a publication. I liked that team members composed their own tweets about articles, so that there was a chance for the tweets in the intervention to have congruent “voice”/style. Pairing tweet-level analytics with content analysis—even as simple as whether a hashtag or an author’s Twitter handle were included—could offer some insight.

Overall, I appreciate this authors’ efforts to untangle questions about how organizational and individual social media promotion might differentially influence viewing (and perhaps reading) of scholarly publications.

On 2017 Mar 26, Atanas G. Atanasov commented:

Excellent review on a very interesting topic, I have featured it at: http://healthandscienceportal.blogspot.com/2017/03/cancer-acidity-and-its-potential-as.html

On 2017 Mar 17, Atanas G. Atanasov commented:

Fascinating work… I have featured this study at: http://healthandscienceportal.blogspot.com/2017/03/stress-induced-despair-behavior-and.html

On 2017 Mar 14, Gabriel Lima-Oliveira commented:

Please access full article free of charge

On 2017 May 03, Lily Chu commented:

I have written a comment which was published on the Annals of Internal Medicine online comments section linked to this article, which can be accessed here:

http://annals.org/aim/article/2607809/cytokine-inhibition-patients-chronic-fatigue-syndrome-randomized-trial

I asked whether the authors had considered subgrouping subjects by infectious/ inflammatory symptoms and comparing their responses to treatment and mention two trials using another cytokine inhibitor (of TNF-alpha), etanercept, in the treatment of ME/CFS. Materials related to those trials can be accessed here:

1. Vallings R. A report from the 5th International AACFS Conference. Availablet at: http://phoenixrising.me/conferences-2/a-report-from-the-fifth-international-aacfs-conference-by-dr-rosamund-vallings.
2. Fluge, O. Tumor necrosis factor-alpha inhibition in chronic fatigue syndrome. Available at: https://clinicaltrials.gov/ct2/show/NCT01730495.

On 2017 Mar 11, Andrew Kewley commented:

I thank the authors for conducting this study and note that such studies are of value even if the outcome is a null result.

While I agree with the overall conclusion that subcutaneous anakinra is ineffective, I carefully note that the published manuscript contains an error.

In the abstract of the article, it states: "At 4 weeks, 8% (2 of 25) of anakinra recipients and 20% (5 of 25) of placebo recipients reached a fatigue level within the range reported by healthy persons."

The closest reference in the body of the manuscript is the following: "In the anakinra group, 2 patients (8%) were no longer severely fatigued after the intervention period (reflected by a CIS-fatigue score <35 [47]), compared with 5 patients (20%) in the placebo group difference, -12.0 percentage points [CI, -31.8 to 7.8 percentage points]; P = 0.22)."

Where the reference [47] was: 47. Wiborg JF, van Bussel J, van Dijk A, Bleijenberg G, Knoop H. Randomised controlled trial of cognitive behaviour therapy delivered in groups of patients with chronic fatigue syndrome. Psychother Psychosom. 2015;84:368-76. [PMID: 26402868] doi:10.1159 /000438867

However the claims made in the abstract refer to healthy ranges, but this is not the same as "severe fatigue" as operationalised by a CIS-fatigue score of less than or equal to 35.

The healthy ranges are instead provided by another study which has also been cited: 41. Vercoulen JH, Alberst M, Bleijenberg G. The Checklist Individual Strength (CIS). Gedragstherapie. 1999;32:131-6.

That study found in a group of 53 healthy controls (mean age of 37.1, SD 11.5) had a mean CIS-fatigue score of 17.3 (SD 10.1). This would provide a cut-off for the "healthy range" of ~27. The manuscript of the present RCT does not provide the results of how many patients met this cut-off score.

Also of note, in a study co-authored by one of the authors of the present study utilised a threshold for a "Level of fatigue comparable to healthy people" as less than or equal to 27.

See: Knoop H, Bleijenberg G, Gielissen MFM, van der Meer JWM, White PD: Is a full recovery possible after cognitive behavioural therapy for chronic fatigue syndrome? Psychother Psychosom 2007; 76: 171–176.

Therefore the claim made in the abstract of patients reaching "a fatigue level within the range reported by healthy persons" is not based on evidence provided in the manuscript, or is simply incorrect. I ask the authors to provide the results of how many patients in both groups met the criteria of having a CIS-fatigue score of less than 27.

On 2017 Mar 08, Lydia Maniatis commented:

The authors discuss “face signals” and “face aftereffects” and “face-selective neurons,” but these terms have no conceptual backing. The underlying basis of the “aftereffects” that have been reported using faces is not known; we could argue (always prematurely) that adaptation to particular contour patterns affects the organization of these contours into faces. To give a parallel, the case of color aftereffects doesn’t license us to posit adaptation of “color-selective” neurons, even though the perception of color is a “high-level” process; we know that they are the perceptual consequences of pre-perceptual, cone-level activity.

The idea of face-selective neurons is highly problematic, as are all claims that visual neurons act as “detectors.” (They are essentially homuncular, among other problems). What, exactly, is being detected? If we draw any shape and stick two dots on it along the horizontal, it becomes a face. It cannot be overstated the extent to which references to visual neural processes in this paper are premature.

With respect to functional explanations, if we don’t know the reason for the effects – again, references to “face-selective neurons” are hopelessly vague and have serious logical problems – then it’s premature to speculate if and what.

All of this seems almost moot given the comments in the discussion that “Our results seemingly contradict those of Kiani et al. (2014), who found that identity aftereffects did decay with time (and that this decay was accelerated when another face was presented between adaptor and test).” The authors don’t know why this is, but speculate that “it is likely that the drastically different temporal parameters between the two studies contributed to the different findings… It is plausible that this extended adaptation procedure would have induced larger and more persistent aftereffects than Kiani et al.'s procedure…. It is plausible that aftereffects resulting from short-term fatigue might recover rapidly with time, whereas aftereffects resulting from more structural changes might be more long-lived and require exposure to an unbiased diet of gaze directions to reset.”

Given that the authors evidently didn’t expect their results to contradict those being discussed, these casual post hoc speculations are not informative. “Plausibility” is not a very high bar, and it is rather subjective. What is clear is that the authors don’t understand (were not able to predict and control for) how variations in their parameters affect the phenomenon of interest.

On 2017 Mar 19, Paul Grossman commented:

Unfortunately, the authors of this paper so far refuse to discuss key most likely severely flawed assumptions of their "recommendations" paper in any open forum available to scientists (here, ResearchGate or PubMed Commons: see their reply to my qnd others's comments in ResearchGate, https://www.researchgate.net/publication/313849201_Heart_Rate_Variability_and_Cardiac_Vagal_Tone_in_Psychophysiological_Research_Recommendations_for_Experiment_Planning_Data_Analysis_and_Data_Reporting )

I have been active in this field for over 30 years. Vagal tone is not "variability in heart rate between inhalation and exhalation"; the latter is termed respiratory sinus arrhythmia (RSA, or also high-frequency heart-rate variability, HRV ) and under very specific conditions may sometimes partially reflect, or be a marker of, cardiac vagal tone. Cardiac vagal tone--on the other hand--is defined as the magnitude of mean heart rate change from one condition to another (e.g. rest to different levels of physical exertion or to pharmacological blockade of parasympathetic control) that is a specific consequence of parasympathetic effects. Obviously the two phenomena are not equivalent: Resipratory sinus arrhythmia is an inherently phasic (not tonic) phenomenon (heart rate shifting rhythmically from inspiration to expiration). Cardiac vagal tone characterizes the average effect of vagal influences upon heart rate during a particular duration of time. Changes in breathing frequency can have dramatic effects upon magnitude of RSA without any effects upon cardiac vagal tone. There are also other conditions in which the two phenomena do not change proportionally to each other: e.g. sometimes when sympathetic activity substantially changes; or when efferent vagal traffic to the heart is blocked by chemicals before it can reach the sinus atrial node; or probably when vagal discharge is so great that the vagal traffic saturates the sinus atrial node leading to profound slowing of heart rate during both inspiration and expiration. These effects are rather clearly shown in the autonomic cardiovascular physiological literature but fail to be acknowledged in much of the psychological or psychophysiological publications. Thus it is plain wrong to believe that RSA is vagal tone. There is really so much evidence that is often systematically ignored, particularly by psychologists working in the field.

On 2017 Mar 13, Paul Grossman commented:

The issue of the influence of respiration (breathing rate and volume) confounding heart-rate variability (HRV) as an index of within-individual changes of cardiac vagal tone remains inadequately covered in this review. My colleagues' and my 1991 and 1993 papers (Grossman , Karemaker & Wieling, 1991; Grossman & Kollai, 1993) using pharmacological blockade controls, rather conclusively show that respiratory sinus arrhythmia (RSA, or high-frequency HRV) under spontaneously varying rates and/or depths of breathing does not provide an accurate reflection of quantitative within-individual variations in cardiac vagal tone. Our results are also clearly far from the only findings demonstrating this fact (see also literature of Saul and Berger, as well as others). Yet this rich resource of findings is neither cited nor addressed in the paper. I would be curious why? The research clearly and consistently shows that when a person's heart rate changes from one condition to another are completely vagally mediated (documenting changes in cardiac vagal tone), changes in RSA WILL NOT ACCURATELY REFLECT those variations in cardiac vagal tone whenever breathing parameters substantially change as well: The alterations in RSA amplitude will be much more closely correlated with respiratory pattern changes, but may not at all reflect vagal tone alterations! The proper method to correct for this issue is, however, another question. The crucial point is that this confound must no longer be swept under the carpet. I welcome any dialogue about this from the authors or others..

A bit simpler explanation: We and others (e.g. Grossman , Karemaker & Wieling, 1991; Grossman & Kollai, 1993; Eckberg, various publications; JP Saul, various publications; R Berger, various publications) have consistently shown that changes in breathing rate and volume can easily and dramatically alter heart-rate variability (HRV) indices of cardiac vagal tone, without actual corresponding changes in cardiac vagal tone occurring! This point is not at all considered in this or many other HRV papers. Any paper purporting to provide standards in this area must deal with this issue. If the reader of this comment is a typically young healthy person, this point can easily be documented by noting your pulse rate as you voluntarily or spontaneously alter your breathing frequency substantially: slow breathing will bring about an often perceptibly more irregular pulse over the respiratory cycle than fast breathing, but there will be little-to-no change in average heart rate over the time (which would almost certainly have to occur for such dramatic perceptible changes in HRV to reflect cardiac vagal tone: heart rate should slow as vagal tone increases, and should speed as vagal tone decreases, provided there are no sympathetic shifts in activity--extremely unlikely in this little experiment!).

On 2017 Mar 07, Paul Brookes commented:

This is an interesting study, but I feel it's a little too close to a study published by my own lab' last year... http://www.jbc.org/content/291/38/20188.abstract

Specifically, several of the findings in this new paper are repeats of findings in our paper (such as the pH sensitive nature of 2HG generation by LDH and MDH, and the discovery that 2HG underlies acid induction of HIF). While it's always great to have your work validated, it's also nice to be CITED when that happens.

Our study was posted on BioRXiv on May 3rd 2016 (http://biorxiv.org/content/early/2016/05/03/051599), 6 weeks before this paper was submitted to Nature Chem Biol. At that time we also submitted to a journal where the senior author here is on the editorial board, only to be rejected. Our paper was finally published by JBC in August, >4 months before the revised version of this current study was submitted.

Furthermore, during the revision of our work, another paper came out from the lab of Josh Rabinowitz, showing 2HG generation by LDH, and also demonstrating pH sensitivity Teng X, 2016. We put an addendum in our JBC paper to specifically mention this work as a "note in added proof". The current paper doesnt' cite the Rabinowitz study either.

On 2017 Aug 15, Varshil Mehta commented:

Thank you very much for this article. Great work.

On 2017 Mar 07, Seán Turner commented:

Strain MCCC 1A03042 is not a type strain of Thalassospira xiamenensis. According to Lai and Shao (2012) [PubMed ID 23209216], strain MCCC 1A00209 is the type.

On 2017 May 16, Sebastien Delpeut commented:

One sentence was accidentally omitted from the acknowledgments.

We thank all laboratory members for continuing support and constructive discussion and Angelita Alcos for technical support.

On 2017 Mar 05, Lydia Maniatis commented:

“The present findings demonstrate that it is difficult to tease apart low-level (e.g., contrast) and midlevel (e.g., transparency) contributions to lightness phenomena in simple displays… Dissociating midlevel transparency explanations from low-level contrast explanations of the crispening effect will always be problematic, as by definition information is processed by “low-level” mechanisms before higher visual processing areas responsible for the midlevel segmentation of surfaces.”

As the above passage indicates, the authors of this article are endorsing the (untenable but common) notion that, within a visual percept, some features are reflections of “low-level” processes, i.e. activities of neurons at anatomical levels nearer to the retinal starting point, while other features are reflections of the activities of “mid-level” neurons, later in the anatomical pathway. Still others, presumably, are reflections of the activities of “high-level” neurons. Thus, when we observe that a grey square on a dark grey background appears lighter than the same grey square on light grey background, this is the result of “low-level” firing patterns, while if we perceive a grey film overlying both squares and backgrounds (an effect we can achieve by simply making certain alterations in the wider configuration, leaving the "target" area untouched), this is a consequence of “mid-level” firing activity. And so on. Relatedly, the story goes, we can effectively observe and analyze neural processes at selected levels by examining selected elements of the percepts to which various stimuli give rise.

These assumptions are not based on any evidence or rational arguments; the arguments, in fact, are all against.

That such a view constitutes a gross and unwarranted oversimplification of an unimaginably complex system whose mechanics, and the relationships between those mechanics and perception, we are not even close to understanding, should be self-evident.

Even if this were not the case, the view is paradoxical. It’s paradoxical for many reasons, but I’ll focus on one here. We know that at any given location in the visual percept – any patch – what is perceived – with respect to any and all features – is contingent on the entire area of stimulation. That is, with respect to the percept, we are not dealing with a process of “and-sum.” This has been demonstrated ad infinitum.

But the invocation of “low-level” processes is simultaneously an invocation of “local” processes. So to say that the color of area “x” in this visual percept is the product of local process “y” is tantamount to saying that for some reason, the normal, organized feedback/feedforward response to the retinal stimulation stopped short at this low-level. But when and how does the system decide when to stop processing at the lower-level? Wouldn't some process higher up, with a global perspective, need to ok this shutting down of the more global process (to be sure, for example, that a more extended view doesn’t imply transparency)? And if so, would we still be justified in attributing the feature to a low-level process?

In addition, the “mid-level segmentation of surfaces” has strong effects on perceived lightness; are these supposed to be added to the “low-level contrast effects” (with the "low-level" info simultaneously underpinning the "mid-level" activity)? A rationale is desperately needed.

Arbitrarily interpreting the visual percept in terms of piecemeal processes for one feature and semi- global processes for another and entirely global processes for a third, and some or all at the same time is not a coherent position.

On 2017 Apr 07, Lydia Maniatis commented:

We can have an interesting conversation right here. Unless you clarify your assumptions, and properly control your variables and sample sizes,further research efforts will be wasted. Every difference in conscious experience is inevitably correlated with differences in physiology. The trick is in how you interpret the inevitable variations in the latter.(At this point in our understanding of brain function, I submit that such efforts are extremely premature.) In your case, you don't even seem to know what experience you are trying to correlate with brain activity.

I believe that your small stimulus duration and the fixation on the red spots may have biased the perception of figure to the corresponding surfaces in older viewers. You clearly don't have a alternative hypothesis that doesn't suffer from serious logical problems (as I noted in an earlier comment).

Peer reviewers are obviously not infallible, which is why this forum exists, and invoking them doesn't count as a counterargument.

On 2017 Apr 06, Jordan W Lass commented:

There are many interesting followups to our work indeed, some of which I believe merit further study. You have begun to identify some of these, and it seems to me there is the possibility for a constructive conversation to be had here. I highly encourage you to stop by our upcoming poster at the Vision Sciences Society conference in Florida in May, where we extend this work by exploring electrophysiological correlates of performance on this task in various conditions in both age groups. Our research group would be happy to discuss the issues you are taking with our work, as well as potentially-fruitful followups that can further address the questions we have raised in this work and that you have touched in some of the above comments.

I believe that, especially due to the presentation of this work over a number of conferences where I was challenged by experts in the field who helped me formulate and refine the ideas presented, as well as the rigorous peer review editorial process leading to the publication of this work in a high quality journal, the rational of our hypothesis and interpretation of our results are clearly laid out in the paper.

Thank you again for your keen interest in this work.

On 2017 Apr 06, Jordan W Lass commented:

None

On 2017 Apr 05, Lydia Maniatis commented:

You say that what you mean by “reduced ability to resolve figure-ground competition…is an open question.” But the language is clear, and regardless of whether concave or convex regions are seen as figure, the image is still being resolved into figure and ground. In other words, your experiments in no sense provide evidence that older people are not resolving images into figure and ground, only that convexity may not be as dispositive a factor as in younger people. Perhaps they are influenced more by the location of the red dot, as I believe that it is more likely that fixated regions will be seen as figure, all other things being equal.

In your response you specify that ‘failure to resolve’ may be interpreted in the sense of “decreased stability of the dominant percept and increased flipping.” However, in your discussion, you note, that, on the contrary, other researchers have found increased stability of the initial percept and difficulty in reversing ambiguous stimuli in older adults. If your inhibition explanation is consistent with BOTH increased flipping and greater stability, then it’s clearly too flexible to be testable. And, again, increased flipping rate is not really the same thing as “inability to resolve.”

The second alternative you propose is that stimuli are “not perceived to have figure ground character, perhaps being perceived as flat patterns.” This is obviously also in conflict with the other studies cited above. If the areas are perceived as adjacent rather than as having a figure-ground relationship, this also involves perceptual organization. For normal viewers, such a percept – e.g. simultaneously seeing both faces and vase in the Rubin vase, is very difficult, so it hard to imagine it occurring in older viewers, but who knows. If such an idea is testable, then you should test it.

You say the logic of your hypothesis is sound and your interpretations parsimonious, but in fact it isn’t clear what your hypothesis is, (what failure to resolve means). If your results are replicable, you may have demonstrated that, under the conditions of your experiment, convex region is less dispositive a factor in older adults. But in no sense have you properly formed or tested any explanatory hypotheses as to why this occurred.

In addition, I don’t think its fair to say that you’ve excluded the possible effect of the brevity of the stimulus. 250ms is still pretty short, considering that saccades typically take about 200ms to initiate. We know that older people generally respond more slowly at any task. The fact that practical considerations make it hard to work with longer exposure times doesn’t make this less of a problem.

On 2017 Apr 04, Jordan W Lass commented:

The interpretation that “differences in the ability to resolve the competition between alternative figure-ground interpretations of those stimuli" comes from the combination of results across experiments, and the literature on figure-ground and convexity context effects in specific. Given that we used a two-alternative forced choice paradigm, which has been commonly used to measure perception even when stimuli are presented below threshold, chance performance is P(convex=figure) = .5. Our observation was regressions to chance in the older group in both convexity bias and CCEs, which is consistent with the interpretation that the older group showed reduced ability to resolve figure-ground competition. Interestingly, as you may be getting at, what "reduced ability to resolve figure-ground" means is an open question: could it be decreased stability of the dominant percept and increased flipping between them or time spent in transition states? could it be that the stimuli are not perceived to have figure-ground character, perhaps being perceived as flat patterns? These are interesting questions indeed, which your idea of adding another response option "no figure-ground observed" is one way of addressing, although it comes with its own set of limitations.

Alternatively, as you propose, it may be the case that the older adults are resolving equally well as younger adults, but with increased tendency of perceiving concave figures compared to the younger group, which would also bring P(convex=figure) closer to .5. However, I can think of no literature or reasoning as to why that would be the case, so I see that as a less parsimonious interpretation. I am intrigued though, and if you are able to develop a hypothesis as to why this would be the case, it could make for an interesting experiment that might shed light into the nature of figure-ground organization in healthy aging.

Critically, the results of Experiment 4 showed a strong CCE in older adults when only concave regions were homogeneously coloured, which is a stimulus class that has been shown to be processed more quickly in younger adults (e.g., Salvagio and Peterson, 2012). Since no conCAVity-context effects were observed when only convex regions were homogeneously coloured (the opposite stimulus properties of the reduced competition stimuli), the Experiment 4 results are strongly supportive of the notion that older adults do show the CCE pattern well-characterized in younger adults, but that the high competition stimuli used in Experiment 1 are are particularly difficult for them to resolve.

The logic of our hypothesis is sound, and our interpretation is the most parsimonious we are aware of based on all the results. Thank you for your question, I would be happy to discuss further if you would like further clarification, or are interested in discussing some of these interesting followups.

On 2017 Apr 04, Lydia Maniatis commented:

If I’m reading this paper correctly, there’s a problem with the logic of the argument.

The finding is that older people are less likely than young people to see convex regions of a stimulus as figure. The authors say that this implies age “differences in the ability to resolve the competition between alternative figure-ground interpretations of those stimuli.”

However, the question they are asking in Exp’t1 is whether a red spot is seen as “on or off the region perceived as figure.” This implies that in every case, one of two border regions is seen as figure; at least, the authors don’t suggest that older people saw neither region as figure - and the question doesn’t allow for this possibility. So my question is, why doesn’t seeing the concave region as figure count as a resolution, inhibitory-competition-wise?

On 2017 Mar 04, Lydia Maniatis commented:

What Ratnasingam and Anderson are doing here is analogous to this imaginary example: Let’s say that I have a strong allergy to food x, a milder one to food y, none to food z, and so on, and that my allergies produce various symptoms. Let’s assume also that some of these effects can be interpreted fairly straightforwardly in terms of formal structural relationships between my immune system and the molecular components of the foods, and others not. For these others, we can assume either a functional rationale or perhaps consider them a side effect of structure or function. We don’t know yet. For other individuals, other allergy/food combinations have corresponding effects. Again, if we know something about the individual we can predict some of the allergic reactions based on known principles.

How much sense would it make now, to conduct a study whose goal is: “to articulate general principles that can predict when the size of an allergic reaction will be large or small for arbitrarily chosen food/patient combinations…. What (single) target food generates the greatest allergic difference when ingested by two arbitrarily chosen patients?” (“Our goal is to articulate general principles that can predict when the size of induction will be large or small for arbitrarily chosen pairs of center-surround displays…. What (single) target color generates the greatest perceptual difference when placed on two arbitrarily chosen surround colors?”)

Furthermore, having gotten their results, our researchers now decline to attempt to interpret them in terms of the nuanced understanding already available.

The most striking thing about the present study is that a researcher who has done (unusually) good work in studying the role of structure and chromatic/lightness relationships in the perception of color is now throwing all this insight overboard, ignoring what is known about these factors and lumping them all together, in the hope of arriving at some magic, universal formula for “simultaneous contrast” that is blind to them. Obviously the effort is bound to fail, and the title – framed as a question, not an answer – is evidence of this. Here is a sample, revealing caveat:

“Finally, it should also be noted that although some of our comparisons involved target–surround combinations in which some targets can appear as both an increment and decrement relative to the two surrounds, which would induce differences in both hue and saturation (e.g., red and green). Such pairs may be rated as more dissimilar than two targets of the same hue (e.g., red and redder), but it could be argued that this does not imply that the size of simultaneous contrast is larger in these conditions. However, it should be noted that such conditions are only a small subset of those tested herein.” Don’t bother us with specifics, we’re lumping.

As the authors discuss in their introduction, studies (treating “simultaneous contrast” in a crude, structure-and-relationship-blind way) produce conflicting results: “The conflicting empirical findings make it difficult to articulate a general model that predicts when simultaneous contrast effects will be large or small, since there is currently no model that captures how the magnitude of induction varies independently of method used…. “ Of course. When you don’t take into account relevant principles, and control for relevant factors, your results will always mystify you.

The conflation between, or refusal to distinguish explicitly, cases in which transparency arises and in which it does not arise is really inexplicable.

"The suggestion that the strongest forms of simultaneous contrast arise in conditions that induce the perception of transparency gains conceptual support from evidence showing that transparency can generate dramatic transformations in both perceived lightness and color..." But the contextual conditions that produce transparency are really quite...transparent...There's no clear reason to lump these with situations that are perceptually and logically distinct.

Also: "In simultaneous contrast displays, the targets and surrounds are also texturally continuous, in the sense that they are both uniform, but there are no strong geometric cues for the continuation of the surround through the target region of the kind known to give rise to vivid percepts of transparency (such as contours or textures). It is therefore difficult to generate a prediction for when transparency should be induced in homogeneous center-surround patterns, or how the induction of transparency should modulate the chromatic appearance of a target as a function of the chromatic difference between a target and its surround."

First, I'll pay him the compliment of saying that I don't think that it would be that difficult for Anderson to generate predictions for when transparency should occur...(I think even I could do it). Second, if this theoretical gap really exists, then this is the problem that should be addressed, not "what happens if we test a lot of random combinations and average the results." It might be useful to take into consideration a demo devised by Soranzo, Galmonte & Agostini (2010) which is a case of transparency effect that lacks the "cues" mentioned here - and thus by these authors' criteria qualifies as a basic simultaneous contrast display. (I don't think its that difficult to explain, but maybe I haven't thought about it enough.)

On 2017 Mar 09, Lydia Maniatis commented:

First, I apologize for the error vis a vis the open-loop experiment.

With respect to "very standard procedures:" Vision science is riddled with references to "standard," "popular," "traditional" "common" "widely used" procedures that have no theoretical rationale. "It is considered safe" is also not a rationale.

With respect to fitting, you calculate r-squared by fitting data in the context of very specific conditions whose selection is without a clear rationale, and thus it is very likely that conditions similar in principle but different in detail would yield different results. For example, you use Gabors, which are widely used but seem to be based on the idea that the visual process performs a Fourier analysis - and a local one at that - for which there are no arguments in favor.

Your findings don't warrant any substantial conclusion. You claim in the paper that: “we have shown that eye and hand movements made toward identical targets can end up in different locations, revealing that they are based on different spatial information.” Only the former claim is true.

Your prior discussion reveals that the conclusions couldn't be more speculative and go far beyond the data : “This difference between hand movements and saccades might reflect the different functional specificity of the two systems… One interpretation of the current results is that there are two distinct spatial maps, or spatial representations, of the visual world.”

Your arguments in favor of this explanation are peppered with casual assumptions: "...the priority for the saccade system might be to shift the visual axis toward the target as fast as possible with little cost for small foveating errors. If integrating past sensory signals with the current input increases processing time (Greenwald, Knill, & Saunders, 2005), the saccadic system might prefer to use current input and maximize the speed of the eye movement. For hand movements instead, a small error might make the hand miss its target with potentially large behavioral costs."

Might + might + might + might (eleven in all in the discussion) means that the effect that you report is far too limited in its implications to warrant the claim you make, quite unequivocally, in your title. Most of your "mights" are not currently testable, and almost certainly represent an overly simplistic view of a system of which we have only the crudest understanding at the neural level. The meaning of the term "sensory signals" also needs clarification, as it also implies a misunderstanding of the nature of perceptual processes.

On 2017 Mar 07, Matteo Lisi commented:

Thanks for the interest in our study.

I invite you to read more carefully the article, the experiment that you indicate as "post-hoc"is actually the open-loop pointing experiment: the details of the method are described at page 4-5, and the results are reported at page 7.

The truncation of response latencies is a very standard procedure, to prevent extreme spurious RTs (e.g. due to anticipation or attention lapses) from being included in the analysis. While there is no universal agreement on the ideal procedure for selecting cut-offs criteria, it is considered safe to use extreme cut-offs that result in the exclusion of only a tiny fraction of trials (<0.5%); see for example the recommendations by Ulrich R, 1994, page 69.

I am confused by your comment regarding the "fitting". The statistical model used in the analysis is a standard multivariate linear regression, with the x, y location of the response as dependent variables. It doesn't require any particular assumption, other than the usual assumptions of all linear models (such as independence of errors, homoscedasticity, normally-distributed residuals), which were not violated in our dataset. These are the same assumptions required also by other common linear models such as simple linear regression and ANOVA.

On 2017 Mar 07, Lydia Maniatis commented:

The discussion of this paper refers to a post hoc experiment whose results apparently used in the analysis of the reported results, but gives details of neither methods nor results, nor any citation. This seems oddly casual:

"To test this hypothesis, we repeated the pointing task in a condition in which vision was blocked during the execution of the movement by means of shutter glasses (open-loop hand pointing), making it impossible to use visual feedback for online correction of the hand movement. The results of this experiment replicated those of the experiment with normal pointing; the only difference was a moderate increase in the variability of finger landing positions, which is reflected in the decreased r2 values of the model used to analyze pointing locations in the open-loop pointing condition with respect to the “normal” pointing condition (see also Figures 1D, E and 2)."

As is usual but hard to understand, an author made up a large proportion of the subjects (1/6), confusing the issue of whether naivete is or is not an important condition to control: "all [subjects] except the author were naïve to the specific purpose of the experiments."

And this:

"In the experiment involving saccades, we excluded trials with latency less than 100 ms or longer than 600 ms (0.36% of total trials); the average latency of the remaining trials was 279.89 ms (SD = 45.88 ms). In the experiment involving pointing, we excluded trials in which the total response time (i.e., the interval between the presentation of the target and the recording of a touch response on the tactile screen) was longer than 3 s (normal pointing: 0.45% of total trials; open-loop pointing: 0.26% of total trials). The average response time in the remaining trials was 1213.53 ms (SD = 351.61 ms) for the experiment with normal pointing and 1004.70 ms (SD = 209.83 ms) for the experiment with open-loop pointing."

It's not clear if this was a post hoc decision, or, whether planned or not, what was the rationale.

As usual, there was a lot of fitting, using assumptions whose rationale is also not clear.

On 2017 Mar 06, Lydia Maniatis commented:

The authors’ theoretical position does not seem coherent. They are making an unintelligible distinction between what they call “low-level” stimulus features – among which they list “brightness, contrast, color or spatial frequency” – on the one hand, and “high-level information such as depth cues.” The latter include “texture and shading.” But in an image, the latter are simply descriptions of perceptual effects of variations in luminance, etc. For example, in a black and white photo what we might refer to as “shading” is objectively changes in the luminance of the surface, and the reaction of our visual system to these variations. Similarly for texture. So when they say that “The perception of depth can have the effect of over-riding some of the salient 2-D cues,” one wonders whether they mean to suggest that the “perception of depth” is based on some kind of clairvoyance. And when they say that “The results lend support to a depth cue invariant mechanism for object inspection and gaze planning” they’re basically just saying “how we look at something depends on what it looks like.” And what it looks like depends on…

With respect to the division of perceptual features into “high-level” and “low-level,” this is also a theoretical non-starter, which I’ve discussed in various comments, including a recent one on Schmid and Anderson (2017), copied below.

The methods are for the most part pre-packaged, from various sources. Their theoretical underpinnings are questionable. The figure 2 example of a face based on texture just doesn’t look like a face at all. We’re told that it was generated using the method described by Liu et al (2005). I guess that will have to do…The use of forced choices is indefensible, resulting in the loss of information and the need to invent untestable “guess rates” and “lapse rates:” “The guessing and the lapse rates were fixed to 0.25 and 0.001, respectively.” The stimuli were vary ambiguous, rendering the recognition task difficult, which necessitated certain post hoc measures to clean up the data. Basically we end up comparing a couple of arbitrary manipulations without any interpretable theoretical significance.

From comment on Schmid and Anderson (2017) https://pubpeer.com/publications/8BCF47A7F782E357ECF987E5DBFC55#fb117951

“The present findings demonstrate that it is difficult to tease apart low-level (e.g., contrast) and midlevel (e.g., transparency) contributions to lightness phenomena in simple displays… Dissociating midlevel transparency explanations from low-level contrast explanations of the crispening effect will always be problematic, as by definition information is processed by “low-level” mechanisms before higher visual processing areas responsible for the midlevel segmentation of surfaces.”

As the above passage indicates, the authors of this article are endorsing the (untenable but common) notion that, within a visual percept, some features are reflections of “low-level” processes, i.e. activities of neurons at anatomical levels nearer to the retinal starting point, while other features are reflections of the activities of “mid-level” neurons, later in the anatomical pathway. Still others, presumably, are reflections of the activities of “high-level” neurons. Thus, when we observe that a grey square on a dark grey background appears lighter than the same grey square on light grey background, this is the result of “low-level” firing patterns, while if we perceive a grey film overlying both squares and backgrounds (an effect we can achieve by simply making certain alterations in the wider configuration, leaving the "target" area untouched), this is a consequence of “mid-level” firing activity. And so on. Relatedly, the story goes, we can effectively observe and analyze neural processes at selected levels by examining selected elements of the percepts to which various stimuli give rise.

These assumptions are not based on any evidence or rational arguments; the arguments, in fact, are all against.

That such a view constitutes a gross and unwarranted oversimplification of an unimaginably complex system whose mechanics, and the relationships between those mechanics and perception, we are not even close to understanding, should be self-evident.

Even if this were not the case, the view is paradoxical. It’s paradoxical for many reasons, but I’ll focus on one here. We know that at any given location in the visual percept – any patch – what is perceived – with respect to any and all features – is contingent on the entire area of stimulation. That is, with respect to the percept, we are not dealing with a process of “and-sum.” This has been demonstrated ad infinitum.

But the invocation of “low-level” processes is simultaneously an invocation of “local” processes. So to say that the color of area “x” in this visual percept is the product of local process “y” is tantamount to saying that for some reason, the normal, organized feedback/feedforward response to the retinal stimulation stopped short at this low-level. But when and how does the system decide when to stop processing at the lower-level? Wouldn't some process higher up, with a global perspective, need to ok this shutting down of the more global process (to be sure, for example, that a more extended view doesn’t imply transparency)? And if so, would we still be justified in attributing the feature to a low-level process?

In addition, the “mid-level segmentation of surfaces” has strong effects on perceived lightness; are these supposed to be added to the “low-level contrast effects” (with the "low-level" info simultaneously underpinning the "mid-level" activity)? A rationale is desperately needed.

Arbitrarily interpreting the visual percept in terms of piecemeal processes for one feature and semi- global processes for another and entirely global processes for a third, and some or all at the same time is not a coherent position.

On 2017 Mar 03, M Mangan commented:

There's a strong response to this by the NASEM. Full version: http://www8.nationalacademies.org/onpinews/newsitem.aspx?RecordID=312017b&_ga=1.59874159.399318741.1481664833

"....The National Academies of Sciences, Engineering, and Medicine have a stringent, well-defined, and transparent conflict-of-interest policy, with which all members of this study committee complied. It is unfair and disingenuous for the authors of the PLOS article to apply their own perception of conflict of interest to our committee in place of our tested and trusted conflict-of-interest policies...."

On 2017 Aug 09, Norberto Chavez-Tapia commented:

Since the first descriptions about pioglitazone treatment in NAFLD we were skeptical, unfortunately at the present time we still lack pharmacological treatment options for this prevalent disease. Despite the favorable results of this manuscript still does not adequately guide clinicians in decision making; based on this we decide to perform trial sequential analysis for assessment of data reliabity in the cumulative meta-analysis; for improvement in advanced cirrhosis for all NASH patients the analysis shows the robustness, reaching the sample size to cross the monitoring boundaries, indicating that the available data is more than enough to sustain the conclusion. This statistical robustness is companied with a number needed to treat for improvement in advanced cirrhosis for all NASH patients of 14 (95% CI 8.9-29.7), and 11 (95% CI 7.2-22) for rosiglitazone-pioglitazone, and pioglitazone respectively. The best candidate for this therapy are those with advanced fibrosis, for this case the number needed to treat is 3 (95%CI 1.8-4.1), and 2 (95%CI 1.4-2.9) for rosiglitazone-pioglitazone, and pioglitazone respectively. The clinical decision should be balanced with the risks described earlier with pioglitazone use, being one of the most relevant the increased risk of bladder cancer (HR of 2.642; 95%CI: 1,106, 6.31, p=0.029) with a number needed to harm of 1200. This data emphasizes the need of suitable assessment of fibrosis, to promote pioglitazone in highly selected patients, which will offer better benefits, reducing exposure to potential adverse effects. Finally, the references in the figures are incorrect, being difficult to follow the original sources.

On 2017 May 22, NephJC - Nephrology Journal Club commented:

This trial on the comparison of peritoneal dialysis versus furosemide in pediatric post-operative acute kidney injury, was discussed on May 23rd and 24th 2017 on #NephJC, the open online nephrology journal club. Introductory comments written by Michelle Rheault are available at the NephJC website here The discussion was quite detailed, with over 90 participants, including pediatric and adult nephrologists and fellows, and joined by author Dave Kwiatkowski. The highlights of the tweetchat were:

• The authors should be commended for designing and conducting this important trial, with funding received from the American Heart Association–Great Rivers Affiliate and the Cincinnati Children’s Hospital Medical Center

• Overall, it was thought to be a well-designed and well-conducted trial, with possible weaknesses being the use of bolus (rather than continuous infusion) of furosemide in the control arm, and the importance of negative fluid balance at day 1 as an important outcome being possible weaknesses

• The results were thought to be quite valid and important, and given the not uncommon risk of acute kidney injury and fluid overload in this setting, that preemptive peritoneal dialysis catheters should be considered more often in children at high risk Transcripts of the tweetchats, and curated versions as storify are available from the NephJC website. Interested individuals can track and join in the conversation by following @NephJC or #NephJC on twitter, liking @NephJC on facebook, signing up for the mailing list, or just visit the webpage at NephJC.com.

On 2017 Nov 28, Natalie Clairoux commented:

Free version of this article available at https://papyrus.bib.umontreal.ca/xmlui/handle/1866/19574

On 2017 Mar 07, Claudiu Bandea commented:

Are the conclusions of the Lancet Neurology article by Stopschinski and Diamond flawed?

In their article entitled “The prion model for progression and diversity of neurodegenerative diseases”(1), Barbara Stopschinski and Marc Diamond conclude: “We do not know if common neurodegenerative diseases (e.g. Alzheimer's disease, Parkinson's disease, ALS and Huntington's disease) involve transcellular propagation of protein aggregation, as predicted by the prion model. Until specific interventions are able to block protein propagation and successfully treat patients, this model will be mainly speculative” (italics and parenthesis added).

Given that one of the authors, Marc Diamond, published several previous articles in which he refers to the primary proteins implicated in neurodegenerative diseases as 'prions' [see for example: “Tau Prion Strains Dictate Patterns of Cell Pathology, Progression Rate, and Regional Vulnerability In Vivo” (2) and “Propagation of prions causing synucleinopathies in cultured cells” (3)], it is surprising to learn in this new article (1) that, in fact, we do not know if these neurodegenerative disorders are caused by 'prions'. Does this mean that there are no “Tau Prion Strains” and there are no “Propagation of prions causing synucleinopathies”?

Also, how do the authors reconcile their conclusion with the following statement in the Abstract of a concurrently published paper entitled “Cellular Models for the Study of Prions”(4): “It is now established that numerous amyloid proteins associated with neurodegenerative diseases, including tau and α-synuclein, have essential characteristics of prions, including the ability to create transmissible cellular pathology in vivo”?

Further, Stopschinski and Diamond state that “until specific interventions are able to block protein propagation and successfully treat patients” the prion model remains speculative. If that’s the case, have these “specific interventions” (which would prove that Alzheimer's, Parkinson's, ALS and Huntington's are indeed caused by ‘prions') been used to also validate that the disorders traditionally defined as ‘prion diseases’, such as Creutzfeld-Jakob disease, are indeed caused by 'prions'? If not, is the prion model for Creutzfeld-Jakob disease just speculative?

In their outline of future directions, the authors write: “Given the wide ranging role of self-replicating protein aggregates in biology, we propose that pathological aggregation might in fact represent a dysregulated, but physiological function of some proteins—ie, the ability to change conformation, self-assemble, and propagate” (1).

This is a remarkable statement in that it points to the radical idea that the pathological aggregation of the proteins implicated in neurodegenerative diseases, such as tau, amyloid β, α-synuclein and ‘prion protein’, is an intrinsic phenomenon associated with their physiological function, which is a profound departure from the conventional view presented in thousands of publications over the last few decades. However, I have a problem with the formulation of the statement, specifically with “…we propose…”. The authors might not be fully familiar with the literature on neurodegenerative diseases, but what they are proposing has been the primary topic of articles published several years ago (e.g. 5, 6).

Given the extraordinary medical, public health and economic burden associated with neurodegenerative diseases, it should be expected for the authors or the editorial team/reviewers (7) to address the questions and issues posted in this comment.

References

(1) Stopschinski BE, Diamond MI. 2017. The prion model for progression and diversity of neurodegenerative diseases. Lancet Neurology. doi: 10.1016/S1474-4422(17)30037-6. Stopschinski BE, 2017

(2) Kaufman SK, Sanders DW, Thomas TL et al. 2016. Tau Prion Strains Dictate Patterns of Cell Pathology, Progression Rate, and Regional Vulnerability In Vivo. Neuron. 92(4):796-812. Kaufman SK, 2016

(3) Woerman AL, Stöhr J, Aoyagi A, et al. 2015. Propagation of prions causing synucleinopathies in cultured cells. Proc Natl Acad Sci U S A. 112(35):E4949-58. Woerman AL, 2015

(4) Holmes BB, Diamond MI. 2017. Cellular Models for the Study of Prions.Cold Spring Harb Perspect Med. doi: 10.1101/cshperspect.a024026. Holmes BB, 2017

(5) Bandea CI. 2009. Endogenous viral etiology of prion diseases. Nature Precedings. http://precedings.nature.com/documents/3887/version/1/files/npre20093887-1.pdf

(6) Bandea CI. 2013. Aβ, tau, α-synuclein, huntingtin, TDP-43, PrP and AA are members of the innate immune system: a unifying hypothesis on the etiology of AD, PD, HD, ALS, CJD and RSA as innate immunity disorders. bioRxiv. doi:10.1101/000604; http://biorxiv.org/content/biorxiv/early/2013/11/18/000604.full.pdf

(7) George S, Brundin P. 2017. Solving the conundrum of insoluble protein aggregates. Lancet Neurol. doi: 10.1016/S1474-4422(17)30045-5. George S, 2017

On 2017 Mar 05, Anders von Heijne commented:

If you like this article, you simply must read this: Lawson AE1, Daniel ES. Inferences of clinical diagnostic reasoning and diagnostic error.J Biomed Inform. 2011 Jun;44(3):402-12. The US philosopher Charles Sanders Peirce has at lot important things to say about how we create our hypotheses!

On 2017 Aug 18, Tamás Ferenci commented:

I congratulate the authors for making the results of Nolte et al much more accessible. To further facilitate the application and investigation of this model, I implemented their reparameterized version under the free and open-source mrgsolve which can be run using R.

The model is available at https://github.com/tamas-ferenci/NolteWeisser_AluminiumKinetics.

On 2017 May 29, Dalia Al-Karawi commented:

Dear Authors, This meta-analysis has previously been published in the Phytotherapy Research Journal since February 2016. The data included in this meta-analysis is identical to the one we published before. The original publication, The Role of Curcumin Administration in Patients with Major Depressive Disorder: Mini Meta-Analysis of Clinical Trials, has included the same studies and quantified the same effect size as you did in this paper. The same goes with the interpretation of data and the conclusions you came up with. I wonder what was your take on this topic that wasn't mentioned before?

On 2017 May 05, Anil Makam, MD, MAS commented:

We thank Dr. Atkin and colleagues for publishing long-term outcomes after a one-time screening flexible sigmoidoscopy.(1) Although we agree that this strategy reduces the relative risk of colorectal cancer (CRC) diagnoses and death, we disagree with the methods the authors used to calculate the absolute magnitude of benefit, which is critical in determining whether screening is actually worth the burden, harms and cost.(2) By relying on per protocol analyses, the authors overestimate the absolute benefit of flexible sigmoidoscopy given healthy user and adherer biases inherent in preventive health interventions— i.e., those who adhere to CRC screening also have other behaviors that reduce their overall risk of cancer and death (e.g. diet, smoking habits, exercise, etc.) independent of the screening test itself.(3, 4) There is strong evidence for the presence of these biases in the UK Flexible Sigmoidoscopy Screening Trial given the marked differences in all-cause mortality within the invited group when stratified by those who were adherent versus those who were not adherent to flexible sigmoidoscopy (20.7% versus 29.5%), a screening test that does not reduce overall mortality. Assessing the absolute benefits for screening from the intention-to-treat analyses gives the most accurate estimates and avoids the pitfalls of these biases. This approach results in markedly attenuated estimates of the benefits (Table). Because screening does not save lives (number needed to screen of infinity for all-cause mortality), accurate estimates of the absolute benefit on reducing CRC diagnoses and CRC-related death are key to informing decision aid development and shared decision making.

See Table here: https://twitter.com/AnilMakam/status/860490959225847809

Anil N. Makam, MD, MAS; Oanh K. Nguyen, MD, MAS

Department of Internal Medicine, UT Southwestern Medical Center, Dallas, Texas, USA

We declare no competing interests.

REFERENCES (1) Atkin W, Wooldrage K, Parkin DM, Kralj-Hans I, MacRae E, Shah U, Duffy S, Cross AJ. Long term effects of once-only flexible sigmoidoscopy screening after 17 years of follow-up: the UK Flexible Sigmoidoscopy Screening randomised controlled trial. Lancet. 2017. (2) Makam AN, Nguyen OK. An Evidence-Based Medicine Approach to Antihyperglycemic Therapy in Diabetes Mellitus to Overcome Overtreatment. Circulation. 2017;135(2):180-195. (3) Shrank WH, Patrick AR, Brookhart MA. Healthy user and related biases in observational studies of preventive interventions: a primer for physicians. J Gen Intern Med. 2011;26(5):546-550. (4) Imperiale TF, Monahan PO, Stump TE, Glowinski EA, Ransohoff DF. Derivation and Validation of a Scoring System to Stratify Risk for Advanced Colorectal Neoplasia in Asymptomatic Adults: A Cross-sectional Study. Ann Intern Med. 2015;163(5):339-346.

On 2017 May 03, Peter Hajek commented:

Meta-analyses do not normally use different approaches than a widely accepted standard and this field has one (see over a dozen Cochrane meta-analyses, Russell Standard, and any other norm in this field). As far as I know, no meta-analysis or individual study over the past 20 years or so included completers only. As explained earlier, the key point is that ‘missingness’ in this field is not considered random. If among 100 smokers who had treatment only 10 answer follow-up calls and report abstinence, the success rate is considered to be 10% rather than 100% as you would report it.

Re: studies that exclude treatment successes, imagine a treatment with good efficacy that helps 50% of patients, but only the 50% that were not helped are followed-up. These treatment failures may have worse outcomes than a random comparator group (they could have been treatment resistant e.g. because they have a more severe condition or other adverse circumstances). Your approach would interpret the finding as showing that the treatment is not only ineffective, but that it causes harm – when in fact it shows no such thing and is simply an artefact of the selection bias.

I appreciate that getting these things right can be difficult and would leave this alone if it was not such an important topic open to ideological misuse. And I agree that more studies are needed for the definitive answers to emerge.

On 2017 Apr 17, Regina El Dib commented:

In his comment, Dr. Hajek states that ‘in smoking cessation trials, drop-outs are classified as non-abstainers;. The approach to dealing with missing data in meta-analysis is differnet from that in trials. A survey of the methods literature identified four proposed approaches for dealing with missing outcome data when conducting a meta-analysis (https://www.ncbi.nlm.nih.gov/pubmed/26202162). All approaches recommended the use of a complete case analysis as the primary analysis. This is exactly how we conducted our meta-analysis (figure 5 in the published paper); the pooled relative ratio (RR) was 2.03 (95% CI 0.94 to 4.38) for smoking cessation with ENDS relative to ENNDS.

The same proposed approaches recommended additional sensitivity analyses using different imputation methods. The main purpose of these additional analyses is to assess the extent to which missing data may be biasing the findings of the primary analysis (https://www.ncbi.nlm.nih.gov/pubmed/23451162). Accordingly, we have conducted two sensitivity analyses respectively assuming that all participants with missing data had success or failure in smoking cessation. When assuming success, the pooled RR was 0.95 (95% CI 0.76 to 1.18, p=0.63) with ENDS relative to ENNDS; when assuming failure, the pooled RR was 2.27 (95% CI 1.04 to 4.95, p=0.04). This dramatic variation in the results when making different assumptions is clearly an indicator that the missingness of data is associated with a risk of bias, and that decreases our confidence in the results. We have already reflected that judgment in our risk of bias assessment of these two studies, in table 4 and figure 2; and in our assessment of the quality of evidence in table 7.

Even if we were going to consider the RR of 2.27 as the best effect estimate (i.e., assuming all those with missing data had failure with smoking cessation), the findings would not be supporting the effectiveness of e-cigarettes on smoking cessation. Indeed, the included trials do not address that question, and our review found no study comparing e-cigarettes to no e-cigarettes. The included trials compare two forms of e-cigarettes.

When assessing an intervention A (e.g., e-cigarettes) that has two types A1 (e.g., ENDS) and A2 (e.g., ENNDS), it would be important to first compare A (A1 and/or A2) to the standard intervention (e.g., no intervention or nicotine replacement therapy (NRT)), before comparing A1 to A2. If A1 and A2 are inferior to the standard intervention with A1 being less inferior than A2 (but still inferior to the standard intervention), focusing on the comparison of A1 to A2 (and ignoring the comparison to the standard intervention) will show that A1 is better than A2. That could also falsely suggest that at least A1 (and maybe A2) is favorable. Therefore, a recommendation of A1 vs. A2 should be considered only if A is already recommended over the standard intervention (i.e. A is non inferior to the standard intervention).

Dr. Hajek also criticizes the inclusion of studies that recruited smokers who used e-cigarettes in the past but continue to smoke. When discussing treatment and examining evidence, we refer to effectiveness (known as pragmatic; a treatment that works under real-world conditions). This includes (among other criteria) the inclusion all participants who have the condition of interest, regardless of their anticipated risk, responsiveness, comorbidities or past compliance. Therefore, the inclusion of studies that recruited smokers who used e-cigarettes in the past but continue to smoke had a role in portraying the impact of ENDS and ENNDS in cigarette smokers on long-term tobacco use.

On 2017 Mar 02, Wasim Maziak commented:

None

On 2017 Mar 02, Peter Hajek commented:

Wow! Let me try to explain these points in turn.

Re excluding drop-outs: Imagine 100 people get real treatment and 40 quit, 100 get placebo and 20 quit. All those who were successful attend for follow up (they feel good, grateful, get praised) but many less among treatment failures are willing to face the music (feel that they disappointed clinicians, may be told off, or feel that treatment was rubbish). If the same proportion of failures attend in each group (or if none attend), the success rate among attenders will be identical for both study arms, despite the real quit rates being 40% vs 20%. Check https://www.ncbi.nlm.nih.gov/pubmed/15733243 I cannot think of a mechanism through which this could act in the opposite way as you assert.

Re including irrelevant studies, your response provided no explanation for doing this.

Re. your statements about 'industry people' who should conduct independent science, I do not have and never had any links with any tobacco or e-cigarette manufacturers; and have published dozens of studies on smoking cessation treatments. I believe that anti-vaping activism presented as science needs challenging because misinforming smokers keeps them smoking and undermining much less risky alternatives to cigarettes protects cigarettes monopoly and harms public health.

On 2017 Mar 02, Wasim Maziak commented:

None

On 2017 Mar 01, Peter Hajek commented:

The conclusion that further trials of e-cigarettes are needed is correct, but there are two major problems with this review of the work that has been done so far.

In smoking cessation trials, drop-outs are classified as non-abstainers because treatment failures are less likely to engage in further contact than treatment successes. Practically all smoking cessation trials and reviews published in the last 10 years or so use this approach. Removing drop-outs from the sample, as was done here, dilutes any treatment effect.

The second serious issue is the inclusion of studies that recruited smokers who used e-cigarettes in the past but continue to smoke. Such studies have a higher proportion of treatment failures in the ‘tried e-cig cohort’ and so have less quitting in this subgroup, but they provide no useful information on the efficacy of e-cigarettes. Saying that they provide low quality evidence is wrong – they provide no evidence at all.

The narrative that some studies show that vaping helps quitting and some that it hinders misrepresents the evidence. No study showed that vaping hinders quitting smoking. The two RCTs with long-term outcome, if analysed in an unbiased way, show a positive effect despite controlling for sensorimotor effects and using low nicotine delivery products.

On 2017 Aug 08, Christopher Tench commented:

Can you possibly provide the coordinates used as it is not possible to understand exactly what analysis has been performed without them.

On 2017 Feb 24, KEVIN BLACK commented:

Nature.com: ... a link to the "MRI-specific module to complement the methods reporting checklist," please?

On 2017 Feb 24, Mary Klem commented:

A primary rationale provided by Cooper et al. for conducting this study is that a previous review (Olatunji et al. 2014) used a search strategy that "was not systematic or clearly defined" (pg 111). Cooper et al. claim that they conducted a systematic search "...following Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA) guidance...(pg 110). However, details provided in the Methods section strongly suggest that Cooper et al. themselves failed to conduct searches that were systematic and that they have failed to provide a clear explanation of what and how they searched. Thus, this review suffers from the same flaws Cooper et al. identified in Olatunji et al 2014.

PRISMA recommends that authors provide, for each database searched, the database name, the platform used to search the database, and the start and end dates for the search of each database. Cooper et al., fail to do this, providing only database names and no start-end dates. They also include EBSCO in the list of databases searched, even though EBSCO is not a database. EBSCO is a platform that can be used to search a variety of databases, and it is not clear from the paper which databases were searched using this platform.

PRISMA also recommends that authors present the complete search strategy used for at least one of the major databases searched. Cooper et al. fail to do this, providing only what appears to be a simple description of their search terms. The authors note that the search terms "were searched in key words, title, abstract, and as MeSH subject headings" (pg 112). This is an odd statement, because the authors say they searched multiple databases, yet MeSH are controlled vocabulary only available for use in PubMed. So did the authors utilize each database's controlled vocabulary e.g., Emtree terms for Embase, PsycINFO thesarus terms? Or did they somehow attempt to use MeSH in these other databases and fail to use the appropriate controlled vocabulary? Given this apparent confusion about the nature of subject headings, I have little confidence that the authors conducted systematic or comprehensive searches.

Overall, then, this review suffers from a lack of clarity about the search strategies used, and the search strategies themselves are suspect. With these limits, it is unlikely that the findings of this study can add to the current literature in any substantive way.

On 2017 Feb 25, Marcia Herman-giddens commented:

It is already known that C6 is not a test for acute LB. This study found "All (34/34) seropositive blood donors followed over time remained seropositive at follow-up after 22-29 months." Perhaps seropositivity remains much longer than this. (Doesn't this question beg for a longer study unless the whole test is thrown out as useless?) This could explain why the older people get the more likely they are to be positive since they would have a longer exposure period ("seroprevalence was significantly higher in males and increased with age"). Males are usually more exposed to the outdoors over a lifetime than women. Thus, it would seem that the conclusion of the study should be that a lot of people have had LB infections in Kalmar County, and that a positive C6 could well indicate ongoing infection or a past infection, rather than the study's implication of false positivity. One wonders who would want blood from a C6 positive donor? The bottom line from this study seems to be that C6 is a useless test for blood screening for LB and should not be used.

On 2017 May 22, Martine Crasnier-Mednansky commented:

The terminology 'induction prevention' does not apply to cAMP-dependent Carbon Catabolite Repression (CCR). It has been used to illustrate CCR in Bacillus subtilis, see figure 2 in Görke B, 2008. Escherichia coli cAMP-dependent CCR does not cause induction prevention. It is therefore incorrect to state: "The current model for glucose preference over other sugars involves inducer exclusion and induction prevention, both of which are strictly dependent on the phosphorylation state of EIIA^Glc in E. coli". Moreover, the major player in induction prevention is HPr, not EnzymeIIA^Glc.

Some referenced papers were misinterpreted by the authors. Lengeler J, 1972 reported, in wild type cells, induction of the mannitol operon 'is not prevented' by glucose. Lengeler J, 1978 reported expression of the mtl operon, in both constitutive and inducible strains, is 'resistant to CCR' caused by glucose. This expression was nearly insensitive to cAMP addition, even though expression of the mtl operon is dependent on cAMP (a cya mutant strain does not grow on mannitol). Hence, the level of cAMP in glucose-growing cells is probably sufficient for expression of the mannitol operon. It is unclear how the authors monitored CCR with their inducible strains, as data were not shown.

It was proposed induction of the mannitol operon may take place in the absence of PTS transport as follows. In the unphosphorylated state, transport of mannitol by Enzyme IICBA^Mtl (MtlA) occurred by facilitated diffusion, upon high-affinity binding of mannitol to the IIC domain Lolkema JS, 1990. Thus, the IIC domain appears as a transporter by itself translocating mannitol at a slow rate. This provides an explanation for the observations that (1) mutant strains lacking Enzyme I and/or HPr were still inducible by mannitol (which originally led to the proposal mannitol may be the inducer of the mannitol operon Solomon E, 1972) and (2) mutant strains lacking Enzyme IICBA^Mtl could not be induced unless mannitol was artificially generated in the cytoplasm. It was therefore concluded mannitol was the inducer of the mannitol operon. Interestingly, in the phosphorylated state, transport of free mannitol by Enzyme IICBA^Mtl can be detected on the condition that the transporter has a poor phosphorylation activity Otte S, 2003.

On 2017 Feb 24, John Roger Andersen commented:

Read publishers pdf version in ReaderCube for FREE: click here.

On 2017 Feb 23, Marko Premzl commented:

The third party data gene data set of eutherian kallikrein genes LT631550-LT631670 was deposited in European Nucleotide Archive under research project "Comparative genomic analysis of eutherian genes" (https://www.ebi.ac.uk/ena/data/view/LT631550-LT631670). The 121 complete coding sequences were curated using tests of reliability of eutherian public genomic sequences included in eutherian comparative genomic analysis protocol including gene annotations, phylogenetic analysis and protein molecular evolution analysis (RRID:SCR_014401).

Project leader: Marko Premzl PhD, ANU Alumni, 4 Kninski trg Sq., Zagreb, Croatia

E-mail address: Marko.Premzl@alumni.anu.edu.au

Internet: https://www.ncbi.nlm.nih.gov/myncbi/mpremzl/cv/130205/

On 2017 Jul 12, Christian J. Wiedermann commented:

After critical reading of the paper, the authors' conclusions suggesting renal safety of hydroxyethyl starch (HES) do not appear warranted. Since BMC Anesthesiology does not offer a correspondence or letters-to-the-editor section, where some of the study's limitations could be discussed, I would like to post a comment here.

Zhang et al. describe a multicenter, double-blind, controlled randomized clinical trial that evaluated the renal safety of HES in patients undergoing hip arthroplasty under spinal anesthesia, apparently showing that there is no increase in renal injury with 6% HES 130/0.4 compared with lactated Ringer’s solution during this type of orthopedic surgery:

• The reported methodology for the study provided no information on the statistical approach, either regarding the sample size calculation or the comparisons between groups for each outcome. Thus, it is impossible to determine whether this study, which involved a relatively small patient population (120 patients randomized), was powered sufficiently to detect statistically significant and clinically important differences between HES and Ringer’s lactate in the primary and secondary outcomes.
• Eligibility criteria meant that the patient population did not include patients with American Society of Anesthesiologists physical status score >III, thus limiting this elderly population to those at a lower risk of developing AKI.
• The primary outcome of the study was the levels of urine and plasma neutrophil gelatinase-associated lipocalin (NGAL) and plasma interleukin 18 (IL-18), which were used as biomarkers for the early detection of AKI. NGAL has been widely investigated as a biomarker for AKI; however, its clinical utility remains unclear because of difficulties in interpreting results due to different settings, sampling time points, measurement methods, and cut-off values [Singer E, 2013]. Although IL-18 holds promise as a biomarker for the prediction of AKI, it has only moderate diagnostic value [Lin X, 2015].
• The follow-up period in the study was only 5 days, and consequently HES-induced AKI may have been missed (the FDA and EMA recommended monitoring of renal function in patients for at least 90 days [Wiedermann CJ, 2017].

Thus, no conclusions regarding the renal safety of HES can be drawn from the study. The assessment of the benefit/risk profile associated with the perioperative administration of HES will require rigorously designed, sufficiently powered randomized controlled clinical trials incorporating a clinically meaningful outcome for the licensed dosage/indication in an appropriate patient population. Most clinical research fails to be useful not because of its findings but because of its design [Ioannidis JP, 2016], which is particularly true for studies with HES [Wiedermann CJ, 2014].

On 2017 Oct 04, william jobin commented:

In the situation where people are using the boats to cross to the island, it is obviously a place to do snail control through periodic weed removal and application of bayluscide. This technique was successfully demonstrated years ago on Volta Lake. Why do you limit yourself to drugs?

On 2017 Nov 27, Harri Hemila commented:

Djulbegovic and Guyatt do not refute my criticism of their 3 novel EBM principles

Djulbegovic and Guyatt challenge my short critique of Djulbegovic B, 2017 by stating that “the BMJ’s rating of EBM as one of medicine’s 15 most important advances since 1840 is but one testimony to the impact of its conceptualization of key principles of medical practice, see BMJ 2007 Jan 20;334(7585):111”.

The short news article to which they refer to has the title “BMJ readers choose the sanitary revolution as greatest medical advance since 1840”.

First, that BMJ news article is a 305-word summary of findings from a Gallup poll of 11341 readers of the BMJ, only one third of whom were physicians. Reporting the opinions of BMJ readers does not refute my criticisms.

Second, the 305-word BMJ text was published in 2007. The BMJ readers could not have anticipated in 2007 the revision of the basic principles of EBM a decade later by Djulbegovic B, 2017. The findings in a 10-year-old survey are not relevant to the current discussion of whether the 3 novel EBM principles are reasonable.

Third, the short BMJ text does not mention the term EBM anywhere in the piece. The text states that “sanitation topped the poll, followed closely by the discovery of antibiotics and the development of anaesthesia.” There are no references to EBM whatsoever.

Fourth, one major proposal of the original EBM-paper in JAMA (1992) was that physicians should not lean uncritically on authorities: “the new [EBM] paradigm puts a much lower value on authority”, see p. 2421 in Evidence-Based Medicine Working Group., 1992. Thus, it is very odd that Djulbegovic and Guyatt argue for the importance of the EBM-approach, while they simultaneously consider that the BMJ is such an important authority. It is especially surprising that the mere reference to a 305-word text in the BMJ somehow would refute my comments, even though the text does not discuss EBM or other issues related to my comments either literally or by implication.

Fifth, Djulbegovic and Guyatt state that the 305-word text in the BMJ is a “testimony” in favor of EBM. Testimonies do not seem relevant to this kind of academic discussion. Testimonies are popularly used when trying to impress uncritical readers about claims to which there is no sound support, such as testimonies for homeopathy on numerous pages in the internet.

Djulbegovic and Guyatt also write “The extent to which EBM ideas are novel or, rather, an extension, packaging and innovative presentation of antecedents, is a matter we find of little moment.”

I do not agree with their view. If there is no novelty in the 3 new EBM principles proposed by Djulbegovic B, 2017, and if there is no reasonable demarcation line between “evidence-based medicine” and “ordinary medicine” or simply “medicine”, why should we reiterate the prefix “evidence-based” instead of simply stating the we are discussing “medicine” and we try to make progress in medicine. If “evidence-based” does not give any added meaning in a discussion, why should such a prefix be used?

Djulbegovic and Guyatt stated that I “do not appear to disagree with [their] overview of the progress in EBM during last quarter of century”. That statement is not entirely correct. A short commentary must have a narrow focus. The focus in my comment was simply on the 3 new EBM principles that were presented by Djulbegovic B, 2017. The absence of any other comments on their overview does not logically mean that I agree with other parts of their overview.

On 2017 Nov 23, BENJAMIN DJULBEGOVIC commented:

Hemila does not appear to disagree with our overview of the progress in EBM during last quarter of century. His main concerns seem to relate to the origin of the ideas. The extent to which EBM ideas are novel or, rather, an extension, packaging and innovative presentation of antecedents, is a matter we find of little moment. The BMJ’s rating of EBM as one of medicine’s 15 most important advances since 1840 is but one testimony to the impact of its conceptualization of key principles of medical practice (see BMJ. 2007 Jan 20; 334(7585): 111.doi: 10.1136/bmj.39097.611806.DB)

Benjamin Djulbegovic & Gordon Guyatt

On 2017 Nov 19, Harri Hemila commented:

The three novel principles for EBM are old: the emperor has no clothes

In their paper, Djulbegovic B, 2017 describe three novel principles for EBM.

Djulbegovic and Guyatt write (p. 416): “the first EBM epistemological principle is that not all evidence is created equal, and that the practice of medicine should be based on the best available evidence.”

There is no novelty in that statement. Even before 1992 scientists including those in the medical fields, understood that some types of research give more reliable answers.

Furthermore, Djulbegovic and Guyatt do not follow the first principle in their own paper. They write (p. 416): “Millions of healthy women were prescribed hormone replacement therapy [HRT] on the basis of hypothesised reduction in cardiovascular risk; randomised trials refuted these benefits and demonstrated that hormone replacement therapy increased the incidence of breast cancer.”

In an earlier paper, Vandenbroucke JP, 2009 wrote “Recent reanalyses have brought the results from observational and randomised studies into line. The results are surprising. Neither design held superior truth. The reasons for the discrepancies were rooted in the timing of HRT and not in differences in study design.” In another paper, Vandenbroucke JP, 2011 wrote “Four meta-analyses contrasting RCTs and observational studies of treatment found no large systematic differences … the notion that RCTs are superior and observational studies untrustworthy … rests on theory and singular events”.

Djulbegovic and Guyatt thus reiterate old assumptions about the unambiguous superiority of RCTs compared with observational studies. They do not follow their own first EBM principle that arguments ”should be based on the best available evidence”. The above mentioned Vandenbroucke’s papers had already been published and were therefore available; thus they should have been taken into account when Djulbegovic and Guyatt argued for the superiority of RCTs in 2017.

Djulbegovic and Guyatt further write (p. 416): “the second [EBM] principle endorses the philosophical view that the pursuit of truth is best accomplished by evaluating the totality of the evidence, and not selecting evidence that favours a particular claim.”

There is no novelty in espousing that principle either. Objectivity has been a long term goal in the natural sciences, and also in the medical fields.

Furthermore, Djulbegovic and Guyatt do not follow the second principle in their own paper. Their reference 94 is to the paper by Lau J, 1992, to which Djulbegovic ja Guyatt refer with the following statement (p. 420): “the history of a decade-or-more delays in implementing interventions, such as thrombolytic therapy for myocardial infarction.” However, in the same paper, Lau J, 1992 also calculated that there was very strong evidence that magnesium was a useful treatment for infarctions with an OR = 0.44 (95% CI: 0.27 - 0.71). However, in the ISIS-4 trial, magnesium had no effects: “Lessons from an effective, safe, simple intervention that wasn't ”, see Egger M, 1995.

Thus, Djulbegovic and Guyatt cherry picked one intervention (trombolytic therapy) to support their statement that many interventions should have been taken into use much more rapidly, but they dismissed another intervention in the paper by Lau J, 1992, that would serve as an unequivocal counter example of the same statement. This surely is an example of “selecting evidence that favours a particular claim”.

Principles 1 ja 2 had already been advocated in James Lind’s book on scurvy (1753), which was listed as reference number 1 in Djulbegovic B, 2017. Lind wrote: “As it is no easy matter to root out old prejudices, or to overturn opinions which have acquired an establishment by time, custom and great authorities; it became therefore requisite for this purpose, to exhibit a full and impartial view of what has hitherto been published on the scurvy; and that in a chronological order, by which the sources of those mistakes may be detected. Indeed, before this subject could be set in a clear and proper light, it was necessary to remove a great deal of rubbish.” See Milne I, 2012.

Thus, Djulbegovic ja Guyatt’s EBM principles 1 and 2 are not new; they are at least over 250 years old.

Djulbegovic and Guyatt write further (p. 416): “the third epistemological principle of EBM is that clinical decision making requires consideration of patients’ values and preferences.”

The importance of patient autonomy is not an innovation that is attributal to EBM, however.

When the EBM-movement started with the publication of the JAMA (1992) paper by the Evidence-Based Medicine Working Group., 1992, there was novelty in the proposals. The suggestion that each physician should himself or herself read original literature to the extent proposed by EBM enthusiasts in 1992 was novel as far as I can comprehend from the history. The strength of the suggestion to restrict to RCTs as the source of valid evidence about the efficacy of medical interventions was also novel as far as I can see. Thus, the Evidence-Based Medicine Working Group., 1992 had novel ideas and described the background for those ideas. We can disagree about the 1992 proposals  as many have done  but I do not consider that it is fair to claim that the JAMA (1992) paper had no novelty.

In contrast, the aforementioned three principles described by Djulbegovic B, 2017 are not novel. The principles can be traced back to times long before even 1992. In addition, none of the principles alone or in combination set any unambiguous demarkation line as to what EBM is in 2017 and what it is not. How does evidence-based medicine differ from “ordinary” medicine, which has been using the same three principles for ages. If there is no difference between the two, why should the “evidence-based” term be used instead of simply writing “medicine”.

In their paper, Djulbegovic and Guyatt also describe their visions for the future, but I cannot see that any of their visions is specific to EBM. We could as well write their visions for future by changing “EBM” to “medicine”.

On 2017 Mar 02, Gwinyai Masukume commented:

In an article he co-authored in The Lancet the late Hans Rosling, internationally acclaimed for giving entertaining and informative videos on global health Maxmen A, 2016, contends the discipline has entered the post-fact era Nordenstedt H, 2016. The article makes a case that in the post-fact era data is tweaked for advocacy purposes, in medical journals, with the inadvertent consequence of misguiding investments needed to achieve the Sustainable Development Goals.

In this article on male circumcision for HIV prevention Downs JA, 2017, it is stated that a “systematic review estimated a risk reduction between 38% and 66%” for female-to-male HIV transmission conferred by voluntary medical male circumcision. It is not clarified whether this risk reduction is absolute or relative although the cited systematic review, in its abstract, remarks it is a relative risk reduction Siegfried N, 2009. An article titled, “Misleading communication of risk” Gigerenzer G, 2010, discusses how such risk communication is non-transparent. By omitting the baseline risk the bigger numbers make better headlines and better advocacy. However, Hans Rosling cautioned against operating on tweaked facts designed for advocacy, especially in medical journals, because journals can easily propagate an inaccurate understanding of the situation which can make fixing global health problems more challenging Maxmen A, 2016 Nordenstedt H, 2016.

On 2017 Nov 07, Victoria MacBean commented:

Plain English Summary:

This study examined differences in children’s awareness of breathing difficulty, specifically the influence of weight and asthma. With obesity on the rise in Western society and asthma being a common long-term medical condition, it is crucial to understand why obese, asthmatic children report more breathlessness than asthmatic children who are not overweight, even when there are no differences in the severity of their asthma. It has previously been suggested that overweight children may have an increased awareness of breathing effort.

This study compared various aspects of breathing across three groups of children: asthmatic children with healthy weight, overweight children with asthma and a control group of healthy weight children. The project involved the children breathing through a device which added resistance to breathing. Children were asked to rate how hard they felt it was to breathe, and the tests also measured the children’s breathing muscle activity to find out how hard the breathing muscles were working as the researchers purposefully increased the children’s effort to breathe.

The anticipated results were that healthy weight asthmatic children and healthy weight children would show similar results, that is that their breathing effort scores would steadily increase as they found it harder to breathe, with the breathing muscles working gradually harder. Meanwhile, the overweight asthmatic children would show a much steeper increase.

From the 27 children who were studied, the results showed that the overweight children gave higher effort scores throughout the tests, but that these increased at the same rate. There were no differences in the way the children’s breathing muscles responded to the tests. The reason for the higher overall effort scores in the overweight asthmatic children was that their muscles are already working harder than the other two groups before the experiment due to the changes that occur in the lung with increased weight. It was then concluded that overweight asthmatic children do not have differences in their awareness of breathing effort, but that their additional body mass means their muscles are already working harder.

This summary was produced by Sarah Ezzeddine, Year 13 student from Harris Academy Peckham, London and Neta Fibeesh, Year 13 student from JFS School, Harrow, London as part of the authors' departmental educational outreach programme.

On 2017 Feb 20, Daniel Corcos commented:

1) What you call"underlying increasing incidence" of breast cancer is the increase due to x-ray induced carcinogenesis. 2) As expected, the major spike of breast cancer incidence (invasive + in situ) is at the end of the 1990's and at the beginning of the 2000's in the USA, contrasting with very few change in women under 50. Similar changes are seen in other countries in the appropriate age group, after implementation of mammography screening.

On 2017 Feb 20, Daniel B Kopans commented:

Response Daniel Corcos' two concerns: 1. Actually, the annual incidence of "true" breast cancers has not been stable. It had been increasing going back to the 1940's. That is the basic point. When women are screened, the cancers detected earlier are layered on top of the increasing baseline. The incidence of invasive breast cancers was increasing in the U.S. and the other countries you mention long before screening became available. .

It is fundamental epidemiology that when screening begins (the prevalence screen) you find the cancers that would have become clinically evident that year PLUS the cancers that were clinically evident that year but over looked PLUS the cancers that are found 1,2, or 3 years earlier by the screening test. Consequently, when new women begin screening the cancers detected (unfortunately called annual incidence) jump up. If this is done in one year (rarely) then it will go up and come down back toward the baseline incidence. If screening continues it never reaches back to the baseline since there will be new women each year having their prevalence screen. In addition, since the incidence of breast cancer increases with age, and screening advances the date of detection (a 47 year old woman will have the incidence of a 49 year old if screening finds cancers 2 years earlier) the annual detection rate will come back down toward the “baseline”, but not reach it. In the U.S. SEER data you can see that the prevalence numbers remained high from the mid 1980’s (when screening began) to 1999 when they turned back down. This is because, in the U.S. the number of women participating in screening steadily increased each year (new prevalence screens) until it plateaued in 1999. This was followed by a decline in the annual detection rate back toward the baseline. However, you will note that the entire SEER curve is tilted up. This is because the baseline was almost certainly increasing by 1% per year over the same time period (as it had been doing going back to 1940). This is why, despite a fairly steady participation in screening after 1999, the annual incidence in 2012 is higher than in 1978. It is not because screening is finding fake cancers, but because the underlying incidence of breast cancer has been steadily increasing. This is evident in other countries as well. 2. Radiation risk to the breast is age related and drops rapidly with increasing age so that by the age of 40 there is no measurable risk at mammographic doses. All of the estimates are extrapolated and even these are below even the smallest benefit from screening. Millions (hundreds of millions??) of mammograms were performed in the 1980’s. If mammography was causing cancers then we would have expected a major spike in breast cancer at the end of the 1990’s (a latency of 8-10 years). Instead, the incidence of breast cancer began to fall in 1999 consistent with the end of the prolonged prevalence peak. Even those who are trying to reduce access to screening no longer point to the radiation risk because there are no data to support it for women ages 40 and over.

On 2017 Feb 20, Daniel Corcos commented:

Clearly, all the evidence for the overdiagnosis epidemics rests on the assumption that the annual incidence of "true" (unable to spontaneously regress) breast cancers is stable after implementation of mammography screening. You acknowledge that breast cancer incidence has increased in the USA after implementation of screening. You should also acknowledge that breast cancer incidence has increased in every country after implementation of screening. This cannot be a coincidence. However, as you have noticed, these cancers must be "true" cancers. So, there is misinformation, but it comes also from those pretending that low-dose x-rays are safe.

On 2017 Feb 19, Alexander Kraev commented:

DOI: 10.1186/1745-6150-9-18