On 2017 Sep 28, Guan-Hua Huang commented:

Dear Dr. Bryson:

Thank you very much for your questions.

The variance between the outcomes registered on clinical trials.gov and those reported in JAMA Surgery resulted from our delay in updating the final project outcomes. Since the original protocol was written in Chinese and did not translate fully to English at the time, our research nurse started with one primary outcome first, and there was a delay in updating the others. Thank you so much for bringing this important omission to our attention. All outcomes have now been accurately registered on clinical trials.gov. In addition, we have now updated and confirmed that the research protocol, which documented all outcomes and was published on the JAMA Surgery website as a supplement, was approved by the institutional review board at the study site.

With regards to the sample size estimation, we were also delayed in posting these results. Initially, we had difficulty finding similar studies to estimate the effect size for delirium, as well as in identifying appropriate methodologic approaches to be used in power analysis for cluster-randomized controlled trials when a binary outcome is modeled. We have now updated to include the power analysis for the cluster continuous outcome and found that 270 patients were required for 80% power, and 360 patients were required for 90% power. In the end, we managed to recruit 377 patients, and post hoc analysis indicated that our study was powered at 81% for delirium.

Thank you for the careful read, and for bringing these important issues to our attention.

We would be glad to answer any further questions.

On 2017 Sep 20, Greg Bryson commented:

Would the authors (or editors) comment on: a) the variance between outcomes registered on ClinicalTrials.gov, those reported in the published manuscript, and those described in the protocol appended as an electronic supplemental file. b) the absence of a formal sample size estimate from the published report (CONSORT 7a) or the protocol (SPIRIT 14). Thank you.

On 2017 Nov 08, Eyal Shahar commented:

“Selection bias without colliders” was… effect‐modification bias x 3

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

On 2017 Nov 22, thomas samaras commented:

Taller people have higher risk of atrial fibrillation, blood clots, pulmonary infarction and abdominal aortic aneurysms. The heart problems of shorter people are not due to inherent biological factors. For example, CHD was rare before the industrial revolution and people were shorter then. In addition, during early 1900s, CHD was low and we were shorter in the US and UK. Women are shorter than men and have lower death rates from heart disease. In addition, many short populations studied in the 20th Century were found to be free of CHD and stroke. Some possible confounders are BMI differences, socioeconomic status, catch-up growth of lower birth weight infants, childhood illnesses which stunt growth and promote adult health problems and poorer quality diets. In addition, shorter people often are more overweight than taller people. Three recent studies by Sohn, Shapiro, and Elsayed found shorter people had lower all-cause and cardiovascular disease mortality.(The Sohn finding for lower CVD was,however, non-significant.)

On 2017 May 28, Philippe Gorphe commented:

Please note that . Hep-2 cell line is HeLa cells so originating from the cervix, . M2e cell line does not exist (actually ATCC can provide Me2 cell line, not M2e, but it is melanoma cell line), . TU212 cell line is a misidentified cell line that is thought not to originate from the larynx https://www.ncbi.nlm.nih.gov/pubmed/21868764

Authors would benefit a strong methodological support in further works

On 2017 Jun 26, Valerio Cozzani commented:

Classification of Aerosols formed in the operation of Heat-not-Burn tobacco products.

“Smoke” is nowadays a term frequently used in colloquial non-technical language to indicate a wide number of different aerosols originated by the combustion or pyrolysis of a material. However, from a technical point of view, due to its importance for fire science, several definitions were adopted to clarify what aerosols should be classified as “smoke” (e.g. see the comprehensive discussions provided by Gross et al. (1967), Mulholland (2008), and Drysdale (2011) to have some examples). A comprehensive definition is given by the National Fire Protection Association (See NFPA 921): smoke is composed of airborne solid and liquid particulates and gases evolved when a material undergoes pyrolysis or combustion, together with the quantity of air that is entrained or otherwise mixed into the mass. Moreover, the above definition clearly remarks that smoke, as evident from the literature, may have a very different chemical and physical nature compared to other aerosols:

1) from a physical point of view it may be composed of solid and liquid particles with different size distributions and concentrations;

2) from a chemical point of view, smoke components may be: i) condensed, liquid combustion products, and/or ii) condensed, liquid products of partial combustion (as high molecular weight and/or low vapor pressure organic liquids formed during fuel primary pyrolysis and volatile emission), and/or iii) solid combustion products (mainly graphitic carbon particles as soot, and inorganic fly ashes), iv) and/or unburned or partially oxidized solid or liquid fuel particles.

Smoke from tobacco combustion has specific features, as reported in reference publications (e.g. see Baker, 2006), and has a very complex composition, including all the above cited chemical components such as: condensed liquid drops of volatiles (tar), soot, and ashes. There is no doubt that the aerosol stream produced by a burning cigarette may be classified as “smoke” according to its definitions reported in the scientific and technical literature.

Recently, Philip Morris International (PMI) developed a heat-not-burn tobacco product, that operates with very different modalities with respect to conventional cigarettes. Even if also in the operation of the heat-not-burn tobacco product an aerosol stream is formed, its classification as “smoke” is not appropriate. The aerosol generated in the PMI heat-not-burn tobacco product is very different in the chemical composition from the smoke formed by the self-sustained smoldering combustion of tobacco in cigarettes and more in general from smoke formed in combustion processes. The aerosol generated in the heat-not-burn tobacco product is composed mainly of water and of products deriving from the evaporation, in the absence of chemical reactions, of substances present in the original tobacco substrate present in the heat-not-burn tobacco product. Even applying the more comprehensive definitions of smoke reported in the literature, these do not apply to the aerosol produced in the operation of such devices, since:

i) experimental data have confirmed that combustion processes are absent in the PMI tobacco product when heated in the heat-not-burn device.

ii) the aerosol produced by the heat-not-burn tobacco product during operation is formed mostly by vaporization phenomena, as proven by the experimental data showing its chemical characterization

iii) very limited low temperature pyrolysis phenomena may be present in the tobacco substrate present in the device during the operation of the heat-not-burn tobacco product (temperatures during operation are lower than 350°C)

Nevertheless, it should be remarked that the above only concerns the correct scientific definition of “smoke” and its applicability to heat-not-burn tobacco products, and that in no way what is written above addresses health issues related to the inhalation of such aerosols.

References

Baker R.R., Smoke generation inside cigarette: Modifying combustion to develop cigarettes that may be less hazardous to health, Progress in Energy and Combustion Science, 32, 373-385, 2006.

Drysdale D., Introduction to Fire Dynamics, 3rd Edition, J.Wiley & Sons Ltd, UK, 2011

Gross D., J.J. Loftus, A.F. Robertson, Method for measuring smoke from burning materials. Symposium on Fire Test Methods – Restraint and Smoke, 1966 ASTM STP 422 (ed. A.F. Robertson), pp. 166–204. American Society for Testing and Materials, Philadelphia, PA.

Mulholland G.W., Smoke production and properties, SFPE Handbook of Fire Protection Engineering, 4th Ed. (Eds Di Nenno et al.), pp. 2.291–2.302. National Fire Protection Association, Quincy, MA, 2008.

National Fire Protection Association, NFPA Glossary of Terms, 2016 Edition, Updated September 23rd 2016, 2016; p.1336. http://www.nfpa.org/codes-and-standards/resources/glossary-of-terms. Last accessed June 26th, 2017.

Valerio Cozzani is Professor of Chemical Engineering at University of Bologna, Italy. This comment is provided on the basis of the results of a scientific evaluation of PMI’s heat-not-burn device committed by PMI

On 2017 May 31, Manuel Peitsch commented:

Philip Morris International (PMI) supports scientific data transparency, data sharing and actively encourages the conduct of independent studies on IQOS that are aimed at advancing scientific and medical knowledge or verifying the results we obtained through our assessment program described by Smith MR, 2016. To date we have published over 30 peer-reviewed articles describing studies specifically conducted with IQOS [1]. We have also submitted a Modified Risk Tobacco Product (MRTP) application with the U.S. FDA [2]. It is important that independent studies are conducted with a high degree of scientific rigor, the same degree of rigor that is expected from our company. Key standards for scientific research are:

1. Studies should be conducted using fit-for-purpose and validated methods
2. Study results should be interpreted in an appropriate and non-misleading manner

As independent scientists are starting to analyze our products, it is perhaps not surprising that different methodologies are applied. We note, for example, that Auer R, 2017 reporting on a chemical analysis of the IQOS aerosol used a “smoking device designed and tested in [their] facility”. Without further description of this system, it is hard to compare their analysis with those we have reported previously, using standard and validated smoking machine systems and procedures. While some of the reported results seem consistent with those that we have previously published, significant points of difference in the described methodologies may account for the disagreements in results obtained by Auer et al. in comparison to our peer-reviewed and published data.

1. Methodologies for smoke and aerosol generation have been amply described in the literature. We are therefore surprised that the authors did not use a recognized smoking regime, but rather used a hybrid between the ISO and the Health Canada Intense (HCI) regime [3], and then used this data to compare their results with those published using the ISO regime (Vu AT, 2015).
2. We were surprised by the measurement results the authors obtained for the volatile organic compounds. For instance, it is perplexing that they report yields of approximately 1 µg acrolein per stick for both IQOS and the cigarette they used in their study. It appears that the acrolein values reported by the authors for the cigarette are 50 times lower than those published by e.g. Health Canada (Hammond D, 2008). Similarly Auer et al. find 10 times lower levels of formaldehyde in cigarettes than Health Canada. Furthermore, the yields of acetone, crotonaldehyde and propionaldehyde are also underestimated.
3. It is generally established that the HCI regime is more relevant to how humans smoke than the ISO regime. Under HCI we find that the reference cigarette 3R4F yields 154±20 µg acrolein per stick (Schaller JP, 2016), which is similar to the 142±17 µg/stick reported by Health Canada. We have also reported that IQOS yields 11±2.36 µg acrolein per stick under HCI. Furthermore, under the ISO, IQOS yields 4.89±0.74 µg acrolein per stick (Schaller JP, 2016).
4. Regarding the polycyclic aromatic hydrocarbons, Auer et al. reported a level of acenaphthene for IQOS that is three fold higher than for cigarettes. Acenaphthene is not part of the list of 58 substances we routinely quantify, nor is it part of any regulatory lists (including the most extensive list, the FDA 93). It is, however, a compound we have measured in the smoke of 3R4F, but could not detect in the IQOS aerosol. Our method is based on mass spectrometry, which is a specific detector, as opposed to the non-specific detection system used by the authors. Their reported level for IQOS may therefore come from an artefact, not linked specifically to acenaphthene.
5. It is also surprising that for many analytes, the reported standard deviations are close to, or even larger than the mean values.
6. Taken together, the above-mentioned issues lead us to question the analytical methods that were used. For future studies we recommend that the authors should reduce the measurement variability between the replicas, validate their methods with a reference cigarette (e.g. 3R4F) and compare their results with those published by a recognized regulatory agency.
7. Unfortunately, the results for carbon monoxide (CO) measurements are reported in ppm (parts per million). We would recommend that they should have been converted to mg/stick. Reporting in the way the authors do precludes a comparison of the measured levels with a standard reference cigarette. In addition, the level of CO for the cigarette was above the measurement range of the used instrument, which precludes a comparison between the IQOS and cigarette yields.
8. Contrary to the authors’ suggestions, “Heat-not-burn” is not an advertising slogan but a shorthand for a product description. We have clearly demonstrated the absence of combustion in IQOS through robust scientific substantiation, which we summarized on PMIscience [1] and in our MRTP application to the U.S. FDA [2]. This has been corroborated by several combustion experts. Furthermore, we have never claimed that IQOS is devoid of pyrolytic processes, which are well known to increase with temperature, and are responsible for much of the remaining HPHCs found in the IQOS aerosol.
9. The authors suggest that we are “dancing around the definition of smoke to avoid indoor-smoking bans”. Unfortunately, the authors did not present any data regarding the impact of IQOS on indoor use. Due to the way in which IQOS functions and is used, its impact on air quality cannot be linearly extrapolated from mainstream aerosol chemistry data. Towards that end, proper indoor air quality studies, using validated methods are needed. One such example can be found in Mitova MI, 2016.
10. PMI has consistently communicated that IQOS aerosol is not devoid of HPHCs, and has transparently published the relative yields of HPHCs in comparison with cigarette smoke. Chemical analysis of the IQOS aerosol shows that it contains on average >90% reduction in the levels of HPHCs when compared with the smoke of the 3R4F reference cigarette. This furthermore leads to a concomitant reduction in cytotoxicity and genotoxicity (Schaller JP, 2016).
11. Since we understand the skepticism around tobacco industry-generated data, we also commissioned an independent, recognized and accredited laboratory to quantify the 58 analytes we routinely measure in our studies [4]. The data was submitted as part of our MRTP application to the U.S. FDA [2].
12. The totality of the evidence collected to date, across a broad range on toxicology, systems toxicology and clinical studies, indicates that IQOS has the potential to present less risk of harm compared to continued smoking for adult smokers who switch to it completely [1].

[1] Smith M, Haziza C, Hoeng J, Lüdicke F, Maeder S, Vanscheeuwijck P and Peitsch MC (2017) The Science behind the Tobacco Heating System: a summary of published scientific articles. Available at: https://www.pmiscience.com/library/pmi-science-ths-executive-summary.

[2] U.S. Food and Drug Administration (FDA). Philip Morris Products S.A. Modified Risk Tobacco Product (MRTP) Applications. May 24, 2017. Available from: https://www.fda.gov/TobaccoProducts/Labeling/MarketingandAdvertising/ucm546281.htm.

[3] Health Canada (2000). Health Canada - Tobacco Products Information Regulations SOR/2000-273, Schedule 2. http://laws-lois.justice.gc.ca/PDF/SOR-2000-273.pdf.

[4] Available at: https://www.pmiscience.com/platform-development/platform-development/aerosol-chemistry-physics/hphcs/levels-hphcs-measured.

Manuel Peitsch is a fully paid employees of PMI, the manufacturer of IQOS.

On 2017 Jul 14, Daniel Weeks commented:

Concerns about the analyses presented in the Han et al (2017) paper have been described by Frank Harrell in his "Statistical Thinking" blog in the "Improper Subgrouping" section of the post entitled "Statistical Errors in the Medical Literature". He points out that this paper "makes the classic statistical error of attempting to learn about differences in treatment effectiveness by subgrouping rather than by correctly modeling interactions. They compounded the error by not adjusting for covariates when comparing treatments in the subgroups, and even worse, by subgrouping on a variable for which grouping is ill-defined and information-losing: age.". For further details and additional concerns, please see the blog post.

On 2017 Jul 05, David Keller commented:

Rationale for performing a per-protocol analysis of this study's data

The percentage of control patients who were switched to statin treatment by their personal physicians reached 29.0 % by the end of the study. Meanwhile, non-adherence to statin therapy grew to 22.2 % in the active treatment group.

Intention-to-treat (ITT) analysis assigns the events experienced by a patient (e.g. death, heart attack) to the group to which the patient was initially randomized, regardless of whether the patient actually took the study medicine (if he was randomized to take it), or whether he took the medicine off-protocol (despite being randomized to the control group). The net effect of these "crossover" events, from control to active treatment, or vice-versa, is to weaken the apparent benefit of the medication, as calculated using ITT. This is good, because as a sort of "worst-case scenario" evaluation, we are assured that, if our patients actually take the study medication, they should probably benefit at least as much as the patients did in the clinical trial.

However, in a case where we are evaluating whether there is really no benefit to a medication, we should also consider a best-case scenario evaluation, because if the medicine is not beneficial even when it is evaluated in a manner which is more highly sensitive for detecting benefit, we can be that much more certain that the study medication has no role in treating the study population.

Per-protocol analysis assigns the outcomes and events experienced by a patient based on his actual behavior during the study. If he crossed over from the control group to active treatment and then had a good outcome, that good outcome would be attributed by per-protocol analysis to the effects of active treatment, not to control treatment. Conversely, if a patient is randomized to active treatment, but never takes a pill, a bad outcome in his case would be "blamed" on the control treatment, not on the study medicine he never took. Per-protocol provides a "best case" scenario evaluation of the study drug; one can think of per-protocol analysis as having increased sensitivity to the benefits of the study medication.

So, in a study like this, it is not enough to perform an intention-to-treat analysis, because all those crossovers might have obscured a significant signal of benefit. It is important to also perform a per-protocol analysis, to assure ourselves that, even in the best of circumstances, the medicine being studied is not beneficial, if even the per-protocol analysis cannot detect benefit.

If per-protocol analysis reveals benefit to the study medication, but intention-to-treat analysis does not show any benefit, then a new study should be conducted, which is better-designed and more carefully executed. In this case, a stronger statin, like atorvastatin, could be tested, and the patients and investigators could be double-blinded, and so on...

On 2017 Jul 05, David Keller commented:

This randomized trial of pravastatin was not blinded, so expectation effects may run rampant

Han and colleagues fail to mention in the above abstract that this randomized study of pravastatin for primary prevention of coronary heart disease and mortality was conducted open-label (unblinded). Blinding of subjects and investigators in clinical trials is required to control expectation effects, which can have an important influence in triggering cardiovascular events. The open-label design of this study is mentioned in the Methods section of the body of the paper, but there is no further discussion of the role of uncontrolled placebo, nocebo, Pygmalion and other expectation effects on the outcome of this study. Why was this study not double-blinded, and how dependable are open-label data for making important clinical decisions regarding statin use?

On 2018 Jan 08, Christopher Southan commented:

This paper was a follow up to the 2004 "Has the yo-yo stopped? An assessment of human protein-coding gene number" https://www.ncbi.nlm.nih.gov/pubmed/15174140

On 2017 Jun 02, Christopher Southan commented:

A revised version is planned in order to incorporate the very useful points raised by the open referees

On 2017 May 25, Prashant Sharma, MD, DM commented:

A read-only version of the paper is available at http://rdcu.be/td4R.

[Author comment] In this series, currently the largest compilation of cases of this entity in literature, we describe the frequencies of three unusual findings on hemoglobin CE-HPLC chromatograms - tiny S-window peaks, small spiky post-HbQ peaks, and split HbA2 peaks, that suggest HbQ-India trait as the likely diagnosis in the north Indian practice setting.

On 2017 Jun 30, Cicely Saunders Institute Journal Club commented:

This paper was discussed at the Cicely Saunders Institute Journal Club on Wednesday 7th June.

This paper reports a well conducted trial of an intervention to improve end of life care in hospitalised elderly people. The authors are to be commended for addressing a clinical priority in a population where end of life care is under-researched.

We discussed this paper in a clinical-academic journal club. Our discussion of the paper was lively and generated a series of reflections on the methods used in the conduct of the trial as well as broader issues relating to the aims and processes of the study intervention.

The long study set up period was considered a strength, enabling participating wards to become accustomed to the data collection procedures before the commencement of the study. We discussed the challenges related to selecting the proxy-reported primary outcome measures, and the potential impact of the unblinded nurses assessing outcomes of care they themselves delivered.

We also discussed whether family recollection of symptom control several weeks into bereavement was a reliable measure of care quality, as it may not capture all the factors contributing to their experience of care, potentially confounding their report. It was suggested that collecting family members’ data via face to face interviews could enhance analysis of the quantitative findings.

The intervention, as reported in this paper, supported by previously published development work, represents a comprehensive effort to improve the quality of care for elderly people dying in hospital settings. The group recognised the challenges and the range of competencies required of hospital medical and nursing staff delivering end of life care. We wondered how the reported changes to the training components of the intervention addressed criticisms of the Liverpool Care Pathway in terms of improving competencies in compassionate communication with families. We discussed the possibility of measuring family care givers experience of receiving safe, compassionate care as an alternative outcome for this intervention.

In their discussion the authors report that qualitative work is to be conducted to explore the findings of the study in more depth, particularly those related to poorer family satisfaction with care in the intervention group. We felt this potential negative effect on families should be investigated before further roll out of the intervention We look forward to reading further outputs from this extensive and commendable body of work.

Commentary by Jo Bayly, Dr Simon Etkind and Dr Wei Gao

On 2017 Aug 14, Stuart RAY commented:

These are substantial concerns - I have written to Professor Nowak to invite comment on this discussion.

On 2017 Jul 29, James M Heilman commented:

Seriously "sea-buckthorn oil protects against infections, prevents allergies, eliminates inflammation and inhibits the aging process". This sounds like world changing news. Looking for the RCTs that back it up and not finding any. The only RCT listed in the refs found NO benefit. https://www.ncbi.nlm.nih.gov/pubmed/23131570 That paper which found NO benefit is used to support this sentence "Sea-buckthorn oil as well as extracts from its fruit are used as an adjunctive therapy in treatment of many diseases". If it has no effect that is not a treatment.

On 2017 Aug 17, Ken G Ryan commented:

Thanks Sarah. Yes you are right of course. This was a typo introduced by the publisher at the last phase of publishing. I tried several times to get them to change it and nothing happened. You will see throughout the paper that the correct epithet is spelled correctly. Its very annoying. Ken

On 2017 Aug 16, Seán Turner commented:

The species epithet 'torques' (sic) is misspelled in the title. The correct species name is Psychroflexus torquis.

On 2017 Jul 07, DANIEL BARTH commented:

The possible role of spike-wave discharges (SWDs) in epilepsy is a highly controversial. Although we expected our work to generate debate, the eLetter from Blumenfeld et al. is disappointing.

For a more detailed response to this eLetter, please see: https://www.dropbox.com/s/d8ut94ayf57f8pk/Response to responseBlumenfeld et al2017.pdf?dl=0

• Partial consciousness and maintenance of cognitive functions during SWD

eLetter: “Their logic appears to be based on the misperception that seizures in absence epilepsy (AE) are always associated with ‘profound impairment of consciousness,’ leading to the flawed premise of the study and its interpretation that anything less than full loss of consciousness must not be AE.”

Loss of conscious is stipulated as an inclusion criterion for diagnosis of typical childhood absence epilepsy, versus mild or no impairment of consciousness as an exclusion criterion (Loiseau and Panayiotopoulos, 2000; Engle, 2013). Accordingly, we characterized WAG/Rij rats as mild absence with partial impairment of consciousness during seizures.

eLetter: “The ‘ability’ to modulate SWD severity in rodent models is not demonstrated since the reduction in number and duration can be explained otherwise.” The alternative explanation put forward is “a sensory cue white noise, which may increase arousal and vigilance known to reduce SWD”.

We stated that operantly conditioned arousal is what terminates SWD bursts early. The possibility that the arousal is due only to the white noise cue, however, fails to account for the critical result that preemptive pellet checks occurred almost entirely in the seconds after each SWD burst, indicating awareness of the SWD, associative learning, and operant control over SWDs.

• SWDs occur in several rodent strains

eLetter: Blumenfeld et al. note SWDs are not observed in most laboratory rodent strains.

That is not correct. Observations of SWDs are common in outbred Sprague Dawley, Long Evans, Wistar and hooded rats. Unlike human absence epilepsy, SWDs become more prevalent with age). Our conclusion is not that SWDs cannot reflect absence epilepsy, but that their ubiquity in various outbred rat strains suggests their unreliability as a signature of absence epilepsy. We have no vested interest in whether SWDs are genetic epilepsy or part of normal rat behavior. We simply recommend caution that Blumenfeld et al. appear opposed to.

eLetter: Single gene mutations can lead to SWDs therefore absence epilepsy. We note that while genes can influence innate rhythms, this does not prove that all SWDs are epileptic or that all SWDs model genetic absence seizures. Furthermore, inbreeding does not seem to be a requirement for SWDs, since our outbred Sprague Dawley rats had the same amount of SWDs as our inbred WAG/Rij rats, and Long Evans rats had approximately four times this amount (Fig. 7).

• SWD/immobility as a model of absence epilepsy

Blumenfeld et al list characteristics that support SWDs as a model of absence epilepsy. We do not understand why they are raising this issue, since we clearly stated that inbred WAG/Rij rats model mild absence seizures in humans.

We believe, however, the case that all SWDs in outbred rats serve to model genetic absence seizures in humans is weak. We and others remain skeptical that most outbred rats have developed - or are developing - absence epilepsy; however, as we said, it is possible.

Conclusion

The eLetter by Blumenfeld et al. was written by experts with decades of publications in absence epilepsy. We have examined many of these papers, plus ones challenging the epileptic nature of SWDs (e.g. Kaplan, 1985; Wiest and Nicolelis, 2003). None of us have studied absence seizures or SWDs, except recently (Rodgers et al., 2015). The research history and publication record of Blumenfeld et al., however, could incline them toward an imbalanced interpretation of our results. We do not understand what specifically were the “overstatements” and inappropriate “assumptions” in Taylor et al. that Blumenfeld et al. claimed in the beginning of their eLetter. We urge readers to re-read our Significance Statement in the context of the eLetter by Blumenfeld et al.: “Our evidence that inbred and outbred rats learn to control the duration of spike–wave discharges (SWDs) suggests a voluntary behavior with maintenance of consciousness. If SWDs model mild absence seizures and/or complex partial seizures in humans, then an opportunity may exist for operant control complementing or in some cases replacing medication. Their equal occurrence in outbred rats also implies a major potential confound for behavioral neuroscience experiments, at least in adult rats where SWDs are prevalent. Alternatively, the presence and voluntary control of SWDs in healthy outbred rats could indicate that these phenomena do not always model heritable absence epilepsy or post-traumatic epilepsy in humans, and may instead reflect typical rodent behavior.”

While writing and revising this manuscript in response to successive peer reviews, we responded to the points of Blumenfeld et al. and tried to objectively incorporate reviewers’ suggestions and avoid misinterpretations of our data. We are disappointed that our efforts were either largely ignored or misrepresented in the eLetter, since this unnecessarily complicates an already controversial subject and detracts from what we believe is the importance of this work.

References

Engle, J, Jr. (2013) Seizures and Epilepsy, 2nd ed. New York ; London: Oxford University Press. Kaplan BJ (1985) The epileptic nature of rodent electrocortical polyspiking is still unproven. Exp Neurol 88:425–436. Loiseau, P, Panayiotopoulos, CP (2000) Childhood absence epilepsy. In: Neurobase. San Diego: Arbor. Rodgers KM, Dudek FE, Barth DS (2015) Progressive, seizure-Like, spike-Wave discharges are common in both Injured and uninjured Sprague-Dawley rats: Implications for the fluid percussion injury model of post-traumatic epilepsy. J Neurosci 35:9194–9204. Wiest MC, Nicolelis MAL (2003) Behavioral detection of tactile stimuli during 7-12 Hz cortical oscillations in awake rats. Nat Neurosci 6:913–914.

On 2017 Jun 29, Antoine Depaulis commented:

This study presents interesting behavioral observations during seizures in absence epilepsy (AE). However, there are many overstatements that could be misinterpreted. This begins with the flawed premise that anything less than full loss of consciousness during spike-wave discharges (SWD) is not AE. The broad group of experts in absence epilepsy who signed this response strongly disagree as outlined below. A more complete collective response can be found at: <https://dl.dropboxusercontent.com/u/3541791/Collective reply to Taylor et al_2017.pdf>

1. Partial consciousness during SWD The authors claim that patients with AE experience "profound loss of consciousness" during seizures. On the contrary, some preservation of consciousness is quite common in human AE. Many clinical studies have shown highly variable responsiveness depending both on task difficulty and vigilance level, even from one SWD to the next in the same individual (Blumenfeld, 2005, Guo et al., 2016). Perception of sensory stimuli, discrimination between relevant and irrelevant stimuli during absence seizures and preservation of some cortical processing has been shown in both rat models and human patients (e.g., Inoue et al, 1992, Chipaux et al., 2013, Berman et al., 2010, Drinkenburg et al., 2003, Guo et al., 2016). In addition, as the authors acknowledge, external stimuli like those in this study can increase vigilance and reduce SWD. Therefore, preserved ability to respond during a task or to modulate seizure severity is not a surprise; instead it provides further support for face validity of rodent SWD for human absence seizures.

2. SWD occur in several rodent strains The occurrence of SWD in some animals from outbred rodent strains has been published many times since the 60’s (Marescaux et al., 1992). However, SWDs are not observed in many individual animals in most inbred or outbred rodent strains (e.g., Letts et al., 2014). For example, when rats with SWD (about 30%) were selected from the initial Wistar colony of Strasbourg to produce the GAERS substrain, about 70 % of the colony did not have SWD and were bred as the non-epileptic control (NEC) strain. No NEC display SWD, even when over one year old (Depaulis et al., 2016). Why SWD are so prevalent in some outbred strains is unknown but might be due to preferential selection of dominantly inherited mutated AE genes in docile animals chosen for breeding. The many examples of single gene mutations in mice that lead to SWD/AE not seen in wild type littermates (Maheshwari and Noebels, 2014), provide further evidence that SWD are not normal in rodents. Some monogenic mutations likely result from genetic drift, such as the spontaneous Gria4 gene mutation causing SWD in C3H/HeJ mice, modulated by SWD suppressor mutations in other genes (Beyer et al., 2008, Frankel et al., 2014). Several additional differences between rodents with or without SWD make it very doubtful that SWD reflect “typical rodent behavior” (see PubMed commons for further details).

3. SWD/immobility as a model of absence epilepsy The authors disregard 4 decades of work firmly demonstrating the face validity, pharmacological predictivity and construct validity of rats and mice with SWD as models for AE (see Jarre et al., 2017 for a recent review).These animals fulfill many features relevant to the human AE (Guillemain et al., 2012). In addition to SWD, immobility and mild facial clonus, rodents models exhibit behavioral, structural, molecular and functional co-morbidities not seen in animals without SWD, but also observed in human patients (Shaw, 2007). Furthermore, the anti-epileptic drug profile in rodent AE models corresponds remarkably well with effects in human patients (Depaulis and van Luijtelaar, 2005, Shaw, 2007, Jarre et al., 2017). Over 20 single gene mutations associated with SWD, have been identified in mice and in rats that are consistent with findings in human AE (Powell et al., 2009, Noebels and Sidman, 1979) (Maheshwari and Noebels, 2014). Finally, many electrophysiological (see Depaulis et al., 2017 for a recent review), and fMRI studies (David et al., 2008, Mishra et al., 2011, 2013) in rat AE models agree with clinical data (Westmijse et al., 2009, Hamandi et al., 2008).

Based on these lines of evidence, we assert that SWD/immobility represents a form of epilepsy in rodents. In our view, these episodes are not a natural behavior nor do all individuals display this trait. Studying SWD, in both outbred and inbred strains as well as single gene mutations, has already enabled 1) the development of predictive models of the efficacy of antiepileptic drug efficacy (Tringham et al., 2012, Marks et al., 2016, Glauser et al., 2017), and 2) enhanced understanding of the pathophysiology of cortico-thalamic circuitry that generates and maintains SWD and the mechanisms underlying associated comorbidities.

Contributors and institutions (by alphabetical order) Hal Blumenfeld, Yale University, New Haven, CT, USA Stéphane Charpier, Pierre and Marie Curie University and INSERM, France Doug Coulter, University of Pennsylvania, Philadelphia, USA Vincenzo Crunelli, Cardiff University, Cardiff, UK. Antoine Depaulis, Grenoble Alpes University and INSERM, France Wayne Frankel, Columbia University, NY, USA Martin J. Gallagher, Vanderbilt University, Nashville, TN, USA John Huguenard, Stanford University, Stanford, CA, USA Cian McCafferty, Yale University, New Haven, CT, USA Richard Ngomba, University of Lincoln, UK Jeffrey Noebels, Baylor College of Medicine, TX, USA Jeanne T. Paz, Univ California & Gladstone Institute of Neurological Disease, San Francisco, USA Terence J. O’Brien, University of Melbourne, Melbourne, Australia Filiz Onat, Marmara University, Turkey Gilles van Luijtelaar, Donders Centre for Cognition, Radboud University, Nijmegen, the Netherlands Laurent Vercueil, Grenoble University Hospital, Neurology Department, Grenoble, France

REFERENCES Berman R et al. (2010) Epilepsia 51:2011–2022. Beyer B et al. (2008) Human Molecular Genetics 17:1738–1749. Blumenfeld H (2005) Epilepsia 46 Suppl 9:21–33. Chipaux M et al. (2013) PLoS One 8:e58180. David O et al. (2008) Plos Biol 6:e315–e2697. Depaulis A, Charpier S (2017) Neurosci Letters 17:30141-6. Depaulis A et al. (2016) J Neurosci Meth 260:159–174. Depaulis A, van Luijtelaar G (2005) In: Models of seizures and epilepsy (Pitkänen A, Schwartzkroin P, Moshe S, eds), pp 233–248. Amsterdam: Oxford: Elsevier Academic. Drinkenburg WHIM et al. (2003) Behavioural Brain Research 143:141–146. Frankel WN et al. (2014) PLoS Genet 10:e1004454. Glauser TA et al. (2017) Ann Neurol 81:444–453. Guillemain I et al. (2012) Epileptic Disord 14:217–225. Guo JN et al. (2016) The Lancet 15:1336-1345 Hamandi K et al. (2008) NeuroImage 39:608–618. Inoue M et al. (1992) Electroencephalogr Clin Neurophysiol. 84:172-9. Jarre G et al. (2017) In: Models of seizure and epilepsy. Second edition (Pitkänen A, Buckmaster P, Galanopoulou AS, Moshe SM, eds). Elsevier, in press. Letts VA et al. (2014) Genes, Brain and Behavior 13:519–526. Maheshwari A, Noebels JL (2014) Monogenic models of absence epilepsy: windows into the complex balance between inhibition and excitation in thalamocortical microcircuits, 1st ed. Elsevier B.V. Marescaux C et al. (1992) J Neural Trans - S35:37–69. Marks WN et al. (2016) Eur J Neurosci 43:25–40. Mishra AM et al. (2013) Epilepsia 54:1214–1222. Mishra AM et al. (2011) J Neurosci 31:15053–15064. Noebels JL, Sidman RL (1979) Science 204:1334–1336. Powell KL et al. (2009) J Neurosci 29:371–380. Shaw FZ (2007) 7-12 Hz J Neurophysiol 97:238–247. Tringham E et al. (2012) Science Transl Med 4:121ra19–121ra19. Westmijse I et al. (2009) Epilepsia 50:2538–2548.

On 2017 Aug 22, Anton Pottegård commented:

On the misleading conclusion reached by Wang et al. regarding use of phosphodiesterase 5 inhibitors and risk of melanoma

Recently, Wang et al. published their findings from a meta-analysis on the putative association between use of phosphodiesterase 5 inhibitors (PDE5i) and risk of melanoma (Wang J, 2017). With this letter, we, the authors of four of the main studies on which their meta-analysis was founded, would like to express our serious concerns as to the conclusions reached by Wang et al.

The initial report on the potential for an association between use of the PDE5i sildenafil and an increased risk of melanoma was published by Li et al. in JAMA Internal Medicine in 2014 (Li WQ, 2014). A large proportion of melanomas contain mutations that lead to suppression of phosphodiesterase enzyme 5A (Gray-Schopfer V, 2007), which again leads to melanoma cell invasion (Arozarena I, 2011). As PDE5is infer a direct pharmacological inhibition of the same enzyme, the hypothesis that use of PDE5i would infer an increased risk of melanoma is biologically plausible.

Four different teams subsequently tried to replicate these findings. In a case-control study using nationwide Swedish health registries, Loeb et al. reported a modest increased risk among PDE5i users (adjusted odds ratio (OR) 1.21, 95% confidence interval (CI) 1.08-1.36) (Loeb S, 2015). However, they clearly pointed out that the association was unlikely to be causal, because there was a lack of dose-response in the observed association (i.e. no increase in risk with greater exposure). Further, the strongest association was observed with early stage melanoma, which lacks biological gradient. Lastly, the authors also observed PDE5i users to have an increased risk of basal cell carcinoma, which was a negative control outcome with no hypothesized association with PDE5i use. This last observation suggested possible confounding by UV exposure, which is the key risk factor for both BCC and melanoma.

The next three studies were published in close succession. Two cohort studies based on data from the UK Clinical Practice Research Datalink (CPRD) found weak evidence of a small increased risk of melanoma among those prescribed a PDE5i (Lian et al (Lian Y, 2016): hazard ratio (HR) 1.18, 95%CI 0.95-1.47); Matthews et al. (Matthews A, 2016): HR 1.14, 95%CI 1.01-1.29). In the study by Lian et al. (Lian Y, 2016), associations were also observed with basal cell and squamous cell carcinoma with respect to certain prescription and pill categories, thereby arguing against a causal association due to lack of specificity. Matthews et al. (Matthews A, 2016) again found no gradient in the association, and observed an association with UV-related negative control outcomes including basal cell carcinoma. They also reported an association between previous solar keratosis and later use of phosphodiesterase inhibitors, strongly suggesting confounding due to PDE5i users having more sun exposure. Lastly, in July 2016, Pottegård et al. (Pottegård A, 2016) published the results of two case-control studies, finding weak evidence of a small positive association in Denmark (OR 1.22, 95%CI 0.99-1.49), and no evidence of an association in the US (OR 0.95, 95%CI 0.78-1.14). Again, no dose-response pattern was found, and as in the analysis by Loeb et al., the highest estimates were obtained for early stage disease.

In summary, all four papers reported a slightly increased risk of malignant melanoma among PDE5i users. Critically, however, all the studies included analyses that probed Hill's criteria for causality (Hill AB, 2015), and the findings of all four studies suggested the association was unlikely to be causal. In summarizing the evidence from these papers, the systematic review by Wang et al. focuses heavily on the single point estimate obtained in their meta-analysis, disregarding the supplementary analyses and the conclusions regarding causality within the individual papers. For this reason, we believe that the conclusions reached by Wang et al. are misleading.

Importantly, Loeb et al. have recently performed a similar meta-analysis to that of Wang et al., arriving at an almost identical point estimate, but with a considerably more informed interpretation (https://doi.org/10.1093/jnci/djx086). While acknowledging the weak positive association between PDE5i use and malignant melanoma, they conclude that the association is unlikely to be causal. Having authored the individual papers, we collectively support this conclusion.

Anton Pottegård (1); Krishnan Bhaskaran (2); Anthony Matthews (2); Laurent Azoulay (3); Pär Stattin (4); Laurel A Habel (5); and Stacy Loeb (6)

(1) Clinical Pharmacology and Pharmacy, Department of Public Health, University of Southern Denmark, Odense, Denmark (2) Faculty of Epidemiology and Population Health, London School of Hygiene and Tropical Medicine, London, UK (3) Department of Epidemiology, Biostatistics, and Occupational Health, McGill University, Montreal, Canada (4) Department of Surgical Sciences, Uppsala University, Uppsala, Sweden (5) Division of Research, Kaiser Permanente Northern California, Oakland, CA, USA (6) Department of Urology and Population Health, New York University, NY, NY, USA

On 2017 Jun 12, John Sotos commented:

West describes angiogenesis, erythropoiesis, and vasoconstriction as clinical sequelae arising from chronically hypoxic tissues at altitude. Another, similar, effect is solid-organ hyperplasia.

In the late 1960s a Peruvian medical student observed several-fold enlargement of the carotid bodies in Andean altitude dwellers (1,2). The degree of enlargment increased with time spent at altitude and, in animal models, reversed after restoration of normoxia(3). Interestingly, this hyperplasia is mediated via endothelin signalling, not by hypoxia-inducible-factors(4).

Tissue hyperplasia may also occur in hypoxic patients at sea level. For example, even before the Peruvian discovery, hyperplasia -- and sometimes malignancy -- of adrenal chromaffin cells, i.e. pheochromocytomas, were described in adults having uncorrected cyanotic congenital heart disease(5). Carotid body cells and adrenal chromaffin cells have similar lineage (from the neural crest) and function (oxygen sensing).

(1) Arias-Stella J. Human carotid body at high altitudes. (Abstract). American Journal of Pathology. 1969; 55: 82a.

(2) Heath D. The carotid bodies in chronic respiratory disease. Histopathology. 1991; 18: 281-283.

(3) Kay JM, Laidler P. Hypoxia and the carotid body. J Clin Pathol Suppl (R Coll Pathol). 1977; 11: 30-44.

(4) Platero-Luengo A, González-Granero S, Durán R, Díaz-Castro B, Piruat J, García-Verdugo JM, Pardal R, López-Barneo J. An O2-Sensitive Glomus Cell-Stem Cell Synapse Induces Carotid Body Growth in Chronic Hypoxia. Cell. 2014; 156, 291–303.

(5) Folger GM, Roberts WC, Mehrizi A, Shah KD, Glancy DL, Carpenter CCJ, Esterly JR. Cyanotic Malformations of the Heart with Pheochromocytoma: A Report of Five Cases. Circulation. 1964; 29: 750-757.

On 2017 Jul 18, Youhe Gao commented:

The strategy I posted here last month was published three years ago on Proteome Sci. 2014 Feb 1;12(1):6. doi: 10.1186/1477-5956-12-6. Fast fixing and comprehensive identification to help improve real-time ligands discovery based on formaldehyde crosslinking, immunoprecipitation an... - PubMed - NCBI https://www.ncbi.nlm.nih.gov/pubmed/24484773

On 2017 Jun 14, Youhe Gao commented:

I found two "overexpression"s in the paper. "Although the extent of bait overexpression is difficult to judge and varies across IP's, previous experimentation has shown that over-expression has little effect on identification of true interacting partners (Sowa et al., 2009)" "VAPBWT overexpression strongly increased the association of EGFP-LSG1 and OSBP with the ER (Figure 7E,G)" Personally, I am not sure if those are enough. In a system, increasing [A] or [B] will lead to more [AB]. As we know more about protein interaction now, this kind of systematic false positive should not be ignored any more. In cells, overexpression with tag may even change the location of the protein. That is why I think the next generation of massive protein interaction studies should start from in vivo crosslinking. I do not want to overemphasize the problem. Most of the protein interactions identified are probably true in cells. The amount of work done is very impressive and respected. I hope users who is using a particular interaction data as the only clue for their future experiment design, maybe they should start with an in vivo crosslinking as a conformation of that interaction. It may make them more confident to proceed.

On 2017 Jun 13, J Wade Harper commented:

These issues have been addressed and discussed in many prior publications (see for example - Cell. 2015 Jul 16;162(2):425-40) and are widely known

On 2017 Jun 09, Youhe Gao commented:

I hope that authors can discuss the impact and possibility of false positive and negative made by tagging, overexpression and washing conditions on protein interactions.

On 2017 May 31, Youhe Gao commented:

This is a great master piece in the field of protein interaction. It is the largest network so far. It is extremely valuable for all biologists. I guess for the authors to reach such a great throughput, using tagging, overexpression and affinity purification was almost inevitable. These procedures could produce some false positives and false negatives. A strategy named 4F-acts was proposed a few years ago trying to minimize false positives and false negatives. Fast Fixation is necessary to study real-time protein-protein interactions under physiological conditions. Fast formaldehyde crosslinking can fix transient and weak protein interactions. With brief exposure to a high concentration of formaldehyde during the crosslinking, the complex is crosslinked only partially, so that the complex is small enough to be resolved by SDS-PAGE, and the uncrosslinked parts of the proteins can be used for identification by shotgun proteomics. Immunoaffinity purification can Fish out complexes that include the proteins of interest. Because the complex is covalently bound, it can be washed as harshly as the antibody-antigen reaction can stand; the weak interactions will remain. Even if the nonspecific binding can persist on the beads or antibody, it will be eliminated at the next step. To Filter out these complexes, SDS-PAGE is used to disrupt non-covalent bonds, thereby eliminating uncrosslinked complexes and simultaneously providing molecular weight information for identification of the complex. The SDS-polyacrylamide gel can then be sliced on the basis of the molecular weight without staining. All the protein complexes can be identified with the sensitivity of mass spectrometry rather than sensitivity of the staining method. The advantages are the following: (i) The method does not involve tagging. (ii) It does not include overexpression. (iii) A weak interaction can be detected because the complexes can be washed as hard as the antigen-antibody reaction can stand as the complexes are crosslinked covalently. No new covalent bond can form as a false positive result. (iv) The formaldehyde crosslinking can be performed at the cellular, tissue, or organ level fast enough so that the protein complexes are fixed in situ in real time. The throughput of this strategy is probably not high enough. But I hope one day a large-scale study can be conducted with it. No matter what, this is a great milestone!

On 2017 Jun 03, J Wade Harper commented:

The results are being loaded now into biogrid. IntAct I believe will take data from biogrid to upload directly.

On 2017 May 29, Christopher Southan commented:

Will these valuable results be loaded into the EBI IntAct Molecular Interaction Database? (http://www.ebi.ac.uk/intact/)

On 2017 Aug 28, Noam Y. Harel commented:

This article has been RETRACTED. It is an obvious plagiarism of Han et al, Annals of Neurology, PMID 26814620. Please see this link: https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5440146/

On 2017 Jun 10, Christopher Southan commented:

This valuable paper would be enhanced by including database links to the structures. In lieu of such, the following URL includes CID links to the 90 TCMD identifiers from Supplementary Data 3 https://www.ncbi.nlm.nih.gov/sites/myncbi/christopher.southan.1/collections/52757717/public/ (this may need a couple of tries for the overloaded Entrez servers). Of these, 26 have vendor matches (maybe more via salt-stripping) and 10 have patent extraction matches (but probably not impinging antinfectives research use)

The final six from Table 1 (3 with vendor matches) are:

TCMDC-123767 = CID 1476278, TCMDC-125445 = CID 44522338, TCMDC-141698 = CID 44536555, TCMDC-141070 = CID 44535609, TCMDC-141154 = CID 44535720, TCMDC-124559 = CID 4782980

https://www.ncbi.nlm.nih.gov/sites/myncbi/christopher.southan.1/collections/52765327/public/

On 2017 Jun 01, Andrea Brancaccio commented:

An interesting and solid biochemical work. As the Authors have stated “the POMTs are suggested to have exquisitely narrow glycosylation functions of α-DG”. As an additional note of some interest, it may be worth considering that POMTs predate dystroglycan. In fact, orthologous members of this family can be found in Capsaspora owczarzaki (Accession: XP004363497) or also in Monosiga brevicollis (Accession: XP001744300) belonging respectively to Filasterea and Choanoflagellata, two unicellular groups, close to early-diverging metazoans, in which dystroglycan had not been found (see Adams JC and Brancaccio A., The evolution of the dystroglycan complex, a major mediator of muscle integrity. Biol Open. 2015 4:1163-79, Adams JC, 2015).

On 2017 Jun 14,     commented:

On behalf of the authors, I would like to refer readers to our recent study that demonstrated reproducibility of the original work after more than 10-years. http://dx.doi.org/10.1016/j.freeradbiomed.2016.10.456

On 2017 May 19, Bastian Fromm commented:

auto-correct affected the name of Hsa-Mir-21

On 2017 May 22, Lydia Maniatis commented:

Part 1 This publication is burdened with an unproductive theoretical approach as well as methodological problems (including intractable sampling problems). Conclusions range from trivial to doubtful.

Contemporary vision science seems determined to take organization of the retinal stimulation out of the picture, and replace it with raw numbers, whether neural firing rates or statistics. This is a fundamental error. A statistical heuristic strategy doesn’t work in any discipline, including physics. For example, a histogram of the relative heights of all the point masses in a particular patch of the world wouldn’t tell anything about the mechanical properties of the objects in that scene, because it would not tell us about distribution and cohesiveness of masses. (Would it tell us anything of interest?)

In perception, it is more than well established that the appearance of any point in the visual field –with respect to lightness, color, shape, etc - is intimately dependent on the intensities/spectral compositions of the points in the surrounding (the entire) field (specifically their effects on the retina) and on the principles of organization that the visual process effectively applies to the stimulation. Thus, a compilation of, for example, the spectral statistics of Purves’ colored cube would not allow us either to explain or predict the appearance of colored illumination or transparent overlays. Or, rather, it wouldn’t allow us to predict these things unless we employed a very special sample of images, all of which produced such impressions of colored illumination. Then we might get a relatively weak correlation. This is because, within this sample, a preponderance of certain wavelengths would tend to correlate with e.g. a yellow, illumination impression, rather than being due, as might be true for the general case, to the presence of a number of unified apparently yellow and opaque surfaces. Thus, we see how improper sampling can allow us to make better (and, I would add, predictable) predictions without implying explanatory power. In perception, explanatory power strictly requires we take into account principles of organization.

In contrast, the authors here take the statistics route. They want to show, or rather, don’t completely fail to corroborate the observation that when surfaces are wet, their look colors are deeper and more vivid, and also to corroborate the fact that changes in perception are linked to changes in the retinal stimulation. Using a set of ready-made images (criteria for the selection of which are not provided), they apply to them a manipulation (among others) that has the general effect of increasing the saturation of the colors perceived. One way to ascertain whether this manipulation causes a surface to appear wet would be to simply ask observers to describe the surface, without any clues to what was expected. Would the surface be spontaneously be described as “wet” or “moist”? This would be the more challenging test, but is not the approach taken.

Instead, observers are first trained on images (examples of which are not provided - I have requested examples) that we are told appear very wet (and the dry versions), and include shape-based cues, such as drops of water or puddles. They are told to use these as a guide to what counts as very wet, or a rating of 5. They are then shown a series of images containing both original and manipulated images (with more saturated colors, but lacking any shape-based cues), and asked to rate wetness from 1 to 5.

The results are messy, with some transformed images getting higher ratings than the originals and others not, though on average they are more highly rated. But the ratings for all the images are relatively low; and we have to ask, how have the observers understood their task? Are they reporting an authentic perception of wetness or moistness, or do they believe are they trying to guess at how wet a surface actually is, based on a rule of thumb adopted during the training phase, in which, presumably, the wet images were also more color-saturated? (In other words, is the task authentically perceptual, or is it more cognitive guesswork?) What does it mean to rate the wetness of a surface at e.g. the “2” level?

The cost of ignoring the factor of shape/structure is evident in the authors’ attempt to explain why the ratings for all images were so low, reaching 4 in only one case. They explain that it may be because their manipulation didn’t include areas that looked like drops or puddles. Does this mean that the presence of drops or puddles actually changes the appearance of the surrounding areas, and/or that perhaps those very different training images included other organized features that were overlooked and that affected perception? Did the training teach observers to apply a cue in practice that by itself produces somewhat different perceptual outcomes? I suppose we could ask the observers about their strategy, but this would muddy the facade of quantitative purity.

At any rate, the manipulation (like most ad hoc assumptions) fails as a tool for prediction, leading the authors to acknowledge that “The image transformation greatly increased the wetness rating for some images but not for others…” (Again, it isn’t clear that “wetness rating” correlates with an authentically perceptual scale). Thus, relative success or failure of the transformation is image-specific, and thus sample-specific; some samples and sample sets would very likely not reach statistical significance. Thus the decision to investigate further (Experiment 1b) using (if I’m reading this correctly) only a single custom-made image that was not part of the original set (on what basis was this chosen?) seems unwise. (This might seem to worsen the sampling problem, but the problem is intractable anyway. As there is no possible sample that would allow the researchers to generate reliable statistics-based predictions for the individual case, any generalization would be instantly falsifiable, and thus lack explanatory power).

The degree to which any conclusions are tied to the specific (and unrationalized) sample is illustrated by the fact that the technical manipulations were tailored to it (from Experiment 1a): “In deciding [the] parameters of the WET transformation, we preliminarily explored a range of parameters and chose ones that did not disturb the apparent naturalness of all the images used in Experiment 1a.” Note the lack of objective criteria for “naturalness.”). (We’re not told on what basis the parameters in Experiment 1b were chosen). In short, I don’t think this numbers game can tell us anything more from a theoretical point of view than casual observation and e.g., trial and error by artists, already have.

On 2017 May 22, Lydia Maniatis commented:

Part !!

The authors also generate a hypothesis via data-digging on the statistics of the images used in 1a. This hypothesis is that greater “hue entropy” is correlated with a larger wetness impression (whatever this may mean given the study’s methods). This is tested with a new set of artificial images made using third-party software, which also are also obviously subject to sampling/confounding problems. Results of manipulating this variable were mixed, with one comparison non-significant, one significant if we apply a relatively low standard (p = 0.04), and one significant at the 0.005 level. So the results are inconclusive, even for this particular sample. The authors note, further, that “the effect of hue entropy cannot be explained by ecological optics” and rationalize their (ambiguous) results in the following very casual and logically incoherent manner:

“Since there is a significant overlap in the distribution of color saturation between dry and wet samples…[t]he key to resolving these ambiguities is to increase the number of samples. When wet-related image features are shared by many different parts in the scene, the image features are likely to be produced by a global common factor, such as wetting. In other words, the more independent colors the scene contains, the more reliably the visual system can judge scene wetness.”

I don’t see why a larger sample would necessarily be a more colorful sample. Also, the authors are suggesting that a larger patch of the visual scene will be more likely to receive a higher wet score than a small patch; this seems very implausible. A Bayesian gloss of this explanation follows, complete with arbitrarily chosen “prior probabilities.” Such a mechanism would render the verisimilitude of human perception highly unreliable on a case-by-case basis, much more so than is the case. The fact is that the visual system doesn’t have to rely on weak probabilities for weakly correlated features when it has much more reliable structural principles to work with.

The description of stimulus as “a natural texture” is not informative from an experimental point of view. The potential choices are infinitely variable.

In the text, the authors are using the term color as though it were an objective feature of the stimulus rather than perceptual factor, which is confusing and should be avoided. (From Wikipedia: “As colorfulness, chroma and saturation are defined as attributes of perception they can not be physically measured as such.”)

Bottom line: 1. Statistical compilations divorced from reference to principles of organization lack explanatory and general predictive power, in perception as in every other discipline. They are not productive tools of scientific discovery.

On 2017 Jun 21, Lydia Maniatis commented:

I don't get it; are citations like these valid? They seem to be doing most of the heavy lifting.

"The finger spread and beauty judgement were recorded by our web app, emotiontracker.com (A.A.B., L. Vale, and D.G.P., unpublished data).

As previous work has shown (A.A.B., L. Vale, and D.G.P., unpublished data), continuous pleasure ratings are well fit by a simple model, refined here ((Equation 1), (Equation 2) ; (Equation 3) and Figure 1B). The model supposes..."

What gives the model assumptions their credibility? Are we supposed to take the claims on faith?

On 2017 Nov 28, Natalie Clairoux commented:

Free version of this article available at https://papyrus.bib.umontreal.ca/xmlui/handle/1866/19572

On 2017 May 21, Amanda Capes-Davis commented:

The authors tested against "two different cancer cell lines", HeLa and KB. Unfortunately this is an example of a misidentified cell line causing confusion. KB is known to be misidentified and is actually HeLa, from cervical cancer, not oral carcinoma as originally reported - so the authors are comparing two samples from the same tumour and individual.

A paper has just been published on the impact of KB in the scientific literature: https://www.ncbi.nlm.nih.gov/pubmed/28455420.

Cell lines are increasingly used by medicinal chemists as models for treatment. The field must consider how to incorporate quality procedures for cell lines as part of manuscript submission if this problem is to be avoided.

A simple check against a list - in this case the ICLAC list of known misidentified cell lines - would have picked up the problem in this instance. See: http://iclac.org/databases/cross-contaminations/

To be confident that misidentification has not occurred, human cell lines should be tested for authenticity using short tandem repeat (STR) profiling. See: http://iclac.org/resources/advice-scientists/

All scientists who use cell lines as models should be aware of guidelines for good cell culture practice. For an example see: https://www.ncbi.nlm.nih.gov/pubmed/25117809

On 2017 May 15, Preben Berthelsen commented:

During light chloroform anaesthesia, 1 of 2500 patients succumbed to sudden cardiac syncope – usually when the skin was incised.

1 in 2000 has a genetically determined defect in repolarisation of the myocardium – the long-QT syndrome. Such patients may likewise succumb to sudden cardiac arrest when experiencing emotional and/or physically stressing events.

The striking similarity in the mode of dying – the sudden unexpected arrest of the heart during stress - makes it a fair hypothesis/assumption that patients dying during chloroform anaesthesia were individuals with an inherited or acquired delay in myocardial repolarisation.

No ECG recording from a patient dying during chloroform anaesthesia exists so the hypothesis cannot be proven.

For 100 years, chloroform was used to alleviate labour pain – remarkably with no maternal deaths. A recent investigation has shown an oestradiol-mediated shortening of the QT-interval - both in normal women and in women with the inherited form of delayed myocardial repolarisation - providing a likely explanation for the safety of the obstetric use of chloroform and lends credence to the hypothesis presented in the paper.

P.G.Berthelsen. MD. Charlottenlund, Denmark

On 2017 May 26, Jafar Kolahi commented:

This is an up-date to the previous research "Kolahi J, Khazaei S. Altmetric: Top 50 dental articles in 2014. Br Dent J. 2016 Jun 10;220(11):569-74. doi: 10.1038/sj.bdj.2016.411."

On 2017 May 23, Stuart RAY commented:

The publisher has now added the URLs to references in the publication.

On 2017 May 13, Stuart RAY commented:

The reference URLs were lost along the way, but here they are (have also asked publisher to add these to the online version):

1 - ORI. Guidelines for responsible data management in research. 2006.

2 - DuBois JM, Chibnall JT, Tait R, Vander Wal J. Misconduct: Lessons from researcher rehab.Nature. 2016;534:173–175. doi: 10.1038/534173a. DuBois JM, 2016

3 - ICMJE. Recommendations for the conduct, reporting, editing, and publication of scholarly work in medical journals 2015.

4 - DHHS. Hipaa privacy rule – research. 2013.

5 - NIH. Grants policy statement. Application and Information Processes. 2016.

6 - NIH. NIH data sharing policy. 2007.

On 2017 May 14, Kiyoshi Ezawa commented:

I think that this commentary is well written overall.

Unfortunately, it lacks some important facts that would have assisted the readers' fair judgements.

So, I have posted my post-publication peer review (PPPR), which also contains the aforementioned facts, onto PubPeer (https://pubpeer.com/publications/0BBC818513066058DB929595CE7C32/comments/120820).

It would be strongly recommended to read the PPPR as well before or after reading this commentary, in order to have unbiased opinions on its subjects.

Kiyoshi Ezawa, Ph.D., the author of references [53,54,55], which are a part of the main subjects of the commentary.

On 2018 Jan 05, Mogens Groenvold commented:

Thank you very much to the Cicely Saunders Institute Journal Club and Javiera Leniz Martelli and Katherine Bristowe for an insightful discussion of key aspects of our article.

Concerning ‘standard care’ in the control group we are currently analyzing and comparing the health care activities in the two groups. This will map the palliative care activities offered outside SPC and clarify whether there was ‘compensation’ in the control group.

Regarding the primary outcome, the most important point to make is that while we did indeed devise and employ a new approach aimed at addressing the issue of heterogeneity in palliative care needs (Johnsen AT, 2013 p. 5 and Johnsen AT, 2014 p. 7), we also carried out a fully conventional analysis. The comparison of these two methods suggested that the new approach was slightly superior (Groenvold M, 2017 p. 822).

In the conventional analysis we compared the change over time between groups according to each of the seven EORTC QLQ-C30 scales selected by our clinicians as the key targets of their SPC. Some of the previous trials found an impact on generic health-related quality of life scales, and we have no reason to believe that our measures are less sensitive (unless our clinicians picked the ‘wrong’ scales; this will be elucidated in a forthcoming analysis of explorative outcomes). Therefore, unfortunately, we do not believe that positive effects have been attenuated in our analysis of the primary outcome.

In relation to the patient sample we agree that just as we sought to minimize heterogeneity in palliative care needs, the heterogeneity in cancer diagnoses should be minimized if the main concern is observe maximal effects on specific problems. However, we aimed at evaluating the impact of SPC in a mixed population of cancer patients with different needs, and, as suggested, a larger sample size may be required for this.

Finally, we agree that the possible lack of uniformity of the intervention between the six SPC units may have weakened the ability to detect a positive effect. Future analyses will elucidate whether the interventions differed between the units.

At this point in time we believe that the two most important explanations of the negative (or, in fact, neutral) trial outcome are that the SPC units may not have had an active, structured approach to early SPC, and that the eight-week trial period was too short. The ongoing analyses are likely to give additional insights.

On 2017 Dec 19, Cicely Saunders Institute Journal Club commented:

This paper was discussed at the Cicely Saunders Institute Journal Club on Wednesday 6th December. We appreciated the opportunity to discuss a well conducted RCT and to see it published even after getting a negative result. We enjoyed discussing this paper and it generated a series of reflections on the methods, in particular regarding the primary outcome.

We positively highlighted the detailed discussion about previous trials regarding early specialist palliative care (SPC) in the introduction, and the clear description of the randomization process as well as the blindness of analysts and the sensitivity analysis. We felt more information about what ‘standard care’ involved for individuals in the control group would have been beneficial.

We discussed extensively the use of patient’s primary need based on the EORTC QLQ-C30 dimensions as primary outcome. We agree with the authors about the importance of addressing the heterogeneity in palliative care patients needs and we value the use of measurements that are important for patients. We wondered if the nature of the outcome chosen required a larger sample size to show a difference between arms. It is clear that some of the dimensions would be easier to modify by a SPC team than others. That makes the positive effect SPC might have had in some dimensions being attenuated in the weighted mean. In addition, SPC might have a different impact according to type of cancer. Including all type of cancer patients increases the variability of the effect, and might require a larger sample size. We wondered if the lack of uniformity of the intervention among the different centres also contributed to lack of significant difference in the primary outcome.

Finally, we valued the discussion of the possible reasons for the lack of effect of the intervention, which need to be taken into account for future trials.

Commentary by Javiera Leniz Martelli and Katherine Bristowe

On 2017 Nov 08, BSH Cancer Screening, Help-Seeking and Prevention Journal Club commented:

The BSH Cancer Screening, Help-Seeking and Prevention Journal Club read with great interest this paper, which we feel provides a useful addition to the literature. In this paper, the authors present a framework for the complex relations between cognition and affect in predicting health behaviour. The authors describe the model that is currently used most often in health behaviour research, which looks at the independent effects of cognition and effect on health behaviour (the “main effects approach”). They then convincingly argue that this model does not consider possible interconnections of thought and feeling and describe three alternative models that may be better at explaining subsequent health behaviour: a mediation model (either an affect-preceding-cognition model or a cognition-preceding-affect model), a moderation model, and a contextualised effects model, which are helpfully explained graphically in the Figure on page 3 of the paper. The authors also provide empirical evidence from the health behaviour literature to support each of these models, and argue that these complex relations should be routinely examined in health behaviour research.

Our group recognised the importance and relevance of this topic to much of our work on the determinants and possible points for intervention in cancer screening, help-seeking, and cancer prevention. The authors provide a good reminder of how theory can be improved to better understand behaviour, which is relevant to our work on, for example, cancer screening as a teachable moment or cancer worry as determinant of screening uptake, but is also applicable to a wide range of other health behaviours such as smoking, exercise, and healthy eating.

However, the paper also raised some questions in our group. First, it was unclear to us which model would be applicable under what circumstances. For example, is this a function of the behaviour or of the affective state that is under study, or could this also be construed as characteristic of an individual or group of individuals? For example, for some people, perhaps those who are more organised or conscientious, the cognition-preceding-affect model may better predict subsequent behaviour, while for others, perhaps those who are struggling to cope due to life difficulties or mental health issues, the affect-preceding-cognition model may better predict behaviour. The authors acknowledge that the models they present are “not mutually exclusive” (p.4), and so “multiple types of relations could be involved in determining engagement in a particular health behaviour” (p.4), but this does not provide much guidance on how these models might guide our formulation of hypotheses to be tested in a particular study. Relatedly, it is unclear how these models can (or should) be applied to existing health behaviour models, and to what extent they require an overhaul of these existing models. Our group noted that the inclusion of these complex relationships could water down existing theoretical models, especially if the specific relationship cannot be identified a priori on theoretical grounds but is a function of the behaviour, affective state, individual, or group under study. From the empirical examples that the authors provide throughout, it is unclear whether the complex relations in those studies were pre-specified based on theoretical grounds, or merely exploratory in nature. In their Discussion on p.11, the authors seem to acknowledge that inclusion of the often-neglected interconnections between cognition and affect will require an exploratory, theory-building approach. Our group would have found it helpful if the authors had provided more practical advice on how to formulate a priori hypotheses about these complex relations, and perhaps some worked examples.

Other questions that were raised by our group are of a more pragmatic nature, such as what the implications of the inclusion of complex relations between cognition and affect would have on study sample size and power (especially if not pre-defined a priori but tested post hoc). A related concern was how to practically take the ideas presented by the authors forward, given that mediation and moderation analyses may require a slightly different skill set, and one that many social scientists may not be very familiar with.

Overall, however, the group felt that these concerns -especially those of a more practical nature- do not override the importance of taking forward the excellent ideas presented in this paper, which could herald a new era for health behaviour research, both in terms of theory and practice.

On 2017 May 26, Hilda Bastian commented:

These are interesting results, showing the critical importance of transparency about trials of pharmaceuticals. However, it does not identify the trials it found, or identify the phases of those trials. It would be helpful if the authors were to release these data, for those interested in the results of this study, anyone interested in doing similar work, and those looking for trials on these particular drugs.

The abstract reports the number of participants in the unpublished trials. It would be good to also provide the number of participants in the published trials.

Note: I wrote a blog post about this study and its context.

On 2017 May 14, Lily Chu commented:

The authors and others might be interested in the following case report from Dr. Nancy Klimas, published in the Journal of Chronic Fatigue Syndrome in 2001. Autologous lymph node transplant was done successfully in one subject with resulting improvements in clinical status and cytokine measurements:

http://www.tandfonline.com/doi/abs/10.1300/J092v08n01_03?journalCode=icfs20

On 2017 Nov 28, Natalie Clairoux commented:

Free version of this article available at https://papyrus.bib.umontreal.ca/xmlui/handle/1866/19528

On 2017 May 15, Lydia Maniatis commented:

Below I comment on some serious conceptual and methodological problems with this publication.

1. Observers are asked to decide which of four briefly presented images is the most blurred, in a forced choice task. Why? The authors tell us that "blur perception is an elemental feature of the human visual system" because it drives accommodation and vergence. The problem, of course, is that we don't perceive the blur driving these responses - at least I don't, as I look around me. So the term "blur perception" isn't valid. In fact, the authors are not talking, here, about the retinal stimulation just preceding and producing proper accommodation etc, but, rather, images that, even post-accommodation, lack sharpness due to the manner in which they were produced or designed. They are asking observers for a conscious assessment of the relationship between an image and the objects of which it might be an imperfect projection. They can call this "blur perception," but this is obviously a very different definition than 'the retinal stimulation preceding accommodation and vergence.' So from a theoretical point of view, I submit that at least the first five paragraphs of this article are irrelevant. The definition of blur perception shifts at paragraph 6, which refers to psychophysical studies. (Given the irrelevance of the exposition, we are left, of course, with the question of the theoretical interest of the present measurements).

2. In paragraph 6, to accommodate the second definition of blur perception, we are referred to "the variance discrimination model of blur." This model "assumes that the visual system is attempting to estimate the local variance of the luminance profile of an image from a set of luminance samples. Each of these samples is, however, perturbed by some level of internal noise or intrinsic blur." The reference to "internal noise or intrinsic blur" is to be taken on faith (and is part of the untenable "signal detection" view of perception, see below). At best, the idea has never been tested and it is not clear how it could be tested. It is my suspicion that adherence to forced-choice paradigms in the area of psychophysics implicitly serves the purpose of ensuring that something that can be interpreted as "noise" (i.e. the shots in the dark by observers) will be present in the data. The same goes for the very brief presentations (which are also uncritically an irrationally assumed to tap into "lower levels" of visual processing).

3. "This model well describes the dipper data and is grounded in signal detection theories of sensory discrimination and decision making (Green & Swets, 1966)." Again, signal detection "theories," are not remotely corroborated or conceptually valid. They date from the sixties when perception was crudely analogized to radar operators trying to decide whether a particular blip was a whale or a ship, and judging from the reference provided have apparently not been further developed since. The "model" along with methods amenable to producing data of the right shape in the context of multiple free parameters and post hoc adjustments was simply adopted uncritically. The concept, with its treatment of neurons as "noisy detectors" has been criticized by Teller (1984). I've discussed the problems in various comments, including here: https://pubpeer.com/publications/8B2F3402AFA4F136252567815CB415. The notion is implicitly homuncular, the homunculus observing neural firing rates at various levels of the visual system and assigning them meaning, presumably via other firing rates...

4. Here's how you explain away discrepancies: "Overall, Intrinsic Blur estimates with our dead leaves stimuli were greater than those reported for border blur discrimination (Watson & Ahumada, 2011) or for blur discrimination with fractal patterns (Mather, 1997), suggesting that blur perception with naturalistic stimuli may be mediated by receptive fields with larger space constants (Mather & Smith, 2002)." It's that easy. Note that the term "naturalistic stimuli" is undefined. Many scholarly perception publications include in this category photos of buildings, sidewalks and shrubbery on college campuses. Not to mention that the "dead leaves" stimulus does not look remotely natural, nor would anyone spontaneously relate it to leaves.

On 2017 May 07, Lydia Maniatis commented:

The major assumption of this article is unviable. That it appears premised wholy on early results of Hubel and Wiesel should be a clue:

“The primary function of the biological visual system is to identify objects in an environment. To achieve this, given that in the earlier stages of visual processing an input image would be decomposed into fragmented components by neural mechanisms with localized receptive fields and specific tuning characteristics (Hubel & Wiesel, 1962, 1968), the visual system must be able to integrate image components into the percept of a coherent object.”

As I discuss in a comment on a different article (positing “curvature detectors”), the idea that neurons at any level of the nervous system may be described as “local detectors” is unviable:

(From https://pubpeer.com/publications/8B2F3402AFA4F136252567815CB415):

“As simple as it may seem, the notion of “curvature-sensitive-filter,” or more generally the notion of neurons as “detectors” is wholly untenable for a number of reasons, including those discussed by Teller (1984). On neurons as detectors: “Single simple cells in area 17 are often described as being triggered by, or detecting, the presence of bars of light at particular orientations [because,] of the stimulus set that has been tried, an oriented bar of light seems to make the cell fire fastest. But to say that the cell has a special role in encoding the stimulus which makes it fire fastest is to commit the same fallacy as to say that a cone with maximum sensitivity at 570 nm is a 570nm detector. It would seem to make more sense to assume that each perceptual element is coded by a pattern of firing among many neurons, and that each different firing rate of each cortical cell is important to the neural code….To use the concept of a trigger feature appears to be to claim implicitly three things: that for any given cortical cell most of the stimuli in the universe are in the null class…that the later elements which receive inputs from the cell ignore variations in the firing rate of the cell and treat the cell as binary…it is hard to set aside the convictions that all of the possible firing rates of cortical cells play a role in the neural code; and that the use of broader universes of stimuli in physiological experiments would reveal the size and heterogeneity of the equivalence classes of neurons….” (p. 1243) The arguments obviously also apply to the case of “curvature-detectors,” for which any correlations to firing rates have not been ascertained, but have only been “modeled” on the basis of a narrow set of stimuli. If the outlines of our RF shapes and circles were constructed of dots, or radiating rays, or shapes producing illusory contours, would the data look different? How would such results connect with the “curvature filter” based model? Would it make sense to make yet more ad hoc models for these cases? The adoption of a particular type of stimulus by many researchers serves to immunize them from inconvenient results and create the illusion of an at least superficially coherent research program.

Teller also challenges explanations based on firing activity of sets of cells at a peripheral level of the visual system, on the basis that it relies implicitly on a “nothing mucks it up” proviso, ignoring as it does questions of how this pattern is maintained through the system or how it constrains more complete models. Given such gaps, this type of explanation, she notes, amounts to little more than a “remote homunculus theory.”

A more subtle (and too little appreciated) problem with Schmidtmann and Kingdom’s claims is that they are confusing perceptual cause and effect. The “curves” we are talking about are perceived curves, not actual, objectively curved objects. There are no curves in the retinal stimulation. As we well know, the presence of a particular form in perception is not a passive response to the retinal stimulation, which at its inception consists of points of contact with photons, but an active construction of forms based on principles the outlines of which may be discerned by the products of the process. There are many examples of geometrical forms delineated by luminance differences that are not perceived, e.g. the stimuli used by Gottschaldt (in Ellis (1938) A Source Book of Gestalt Psychology ) and demonstrations by Kanizsa (1979, Organization in Vision). So to say that neurons are detecting curve maxima and minima is basically to say that a form that is first constructed by the visual system, on the basis of dynamic feedback and feedforward mechanisms which we are not even close to understanding, are brought to consciousness, and are secondarily inspected and by a set of detectors said to live at some arbitrary level of the process, which signal the conscious observer in some cryptic way. Again, it’s a hall of mirrors. “

In addition, one could note that, given the massive interconnectedness and interaction of the visual system, when Hubel and Wiesel were recording from particular neurons in V1 they were in effect recording from the whole visual process. That is, it is not possible to claim that these recordings were isolating the independent behavior of these particular neurons.

In addition to the premise that neurons in the visual system act as “local linear detectors” another underlying premise that has zero theoretical support is that the conditions, stimuli and data of these experiments are such as to allow them to be used to infer the behavior of such detectors at specific locations of the visual system. Of course, as Graham (1992) has admitted, hundreds of threshold studies “consistent” with the gross over-interpretation of Hubel and Wiesel’s early results (at a time when V1 was thought to be all there was) were generated in the ensuing decades. This is just one of the latest.

As usual in this type of study, the number of observers is very small (3), two are described as naïve but the third is an author, i.e. not naïve. If naivete matters, then why an author/subject?

As usual in this type of study, a “model,” involving untested or false premises and various atheoretical free parameters, is constructed post hoc, narrowly tailored to the specific dataset, stimuli and conditions. Observations on all other stimuli, conditions fall outside its purview.

As is usual in this type of study, we are given very detailed descriptions of stimuli and conditions, but no indication of their theoretical necessity, and how data and interpretation would change if they were even slightly altered. Relatedly it was interesting to note that stimuli were exposed for 167ms, the identical interval used by Wilson and Wilkinson (1998). What is special about this interval?

“It is known that the visual system cannot group two dots of opposite luminance polarities into a dipole [dot pair] (Glass & Switkes, 1976; J. A. Wilson et al., 2004).” I’m sure this isn’t true. Even if they are the only two dots in the visual field, we will see a pair of dots.

The intellectual level of theorizing in this line of research is exemplified by the elevation of the observation that like figures tend to be grouped together in the visual percept (as in the case of the classic Gestalt dot demos) into “similarity theory.” (Casually tacking on the word “theory” to observations of effects is typical in psychology in general.) Similarity isn’t the only factor mediating organization of the visual stimulus.

On 2017 May 06, Hilda Bastian commented:

The conclusion that implicit bias in physicians "does not appear to impact their clinical decision making" would be good news, but this systematic review does not support it. Coming to any conclusion at all on this question requires a strong body of high quality evidence, with representative samples across a wide range of representative populations, using real-life data not hypothetical situations. None of these conditions pertain here. I think the appropriate conclusion here is that we still do not know what role implicit racial bias, as measured by this test, has on people's health care.

The abstract reports that "The majority of studies used clinical vignettes to examine clinical decision making". In this instance, "majority" means "all but one" (8 out of 9). And the single exception has a serious limitation in that regard, according to Table 1: "pharmacy refills are only a proxy for decision to intensify treatment". The authors' conclusions are thus related, not to clinical decision making, but to hypothetical decision making.

Of the 9 studies, Table 1 reports that 4 had a low response rate (37% to 53%), and in 2 studies the response rate was unknown. As this is a critical point, and an adequate response rate was not defined in the report of this review, I looked at the 3 studies (albeit briefly). I could find no response rate in any of the 3. In 1 of these (Haider AH, 2014), 248 members of an organization responded. That organization currently reports having over 2,000 members (EAST, accessed 6 May 2017). (The authors report that only 2 of the studies had a sample size calculation.)

It would be helpful if the authors could provide the full scoring: given the limitations reported, it's hard to see how some of these studies scored so highly. This accepted manuscript version reports that the criteria themselves are available in a supplement, but that supplement was not included.

It would have been helpful if additional important methodological details of the included studies were reported. For example, 1 of the studies I looked at (Oliver MN, 2014) included an element of random allocation of race to patient photos in the vignettes: design elements such as this were not included in the data extraction reported here. Along with the use of a non-validated quality assessment method (9 of the 27 components of the instrument that was modified), these issues leave too many questions about the quality rating of included studies. Other elements missing from this systematic review (Shea BJ, 2007) are a listing of the excluded studies and assessing the risk of publication bias.

The search strategy appears to be incompletely reported: it ends with an empty bullet point, and none of the previous bullet points refer to implicit bias or the implicit association test.

On 2017 May 25, William McBride commented:

We have concerns that this paper overestimates the risk of dengue transmission through reliance on a test inadequately specific for blood donor screening. An earlier study of 100 donors from the same group Ashshi AM, 2015 acknowledged that the absence of molecular confirmation was a weakness of that study, but they utilised the same methods in this larger group. A similarly sized study conducted in Australia Rooks K, 2016 showed that of 973 donors tested, 3.3% were positive using the PanBio NS1 assay, but that no samples were positive using the BioRad NS1 assay. Further testing of over 6000 blood samples collected during 2 outbreaks were negative using a nucleic acid amplification assay. The question of the proportion of patients who remain asymptomatic during dengue infection is important, not just for assessing risk from blood donors, but for better understanding transmission of dengue more widely. A recent contribution in our understanding of the importance of asymptomatic dengue in transmission dynamics can be found at Duong V, 2015 which showed that around 7% of people infected with dengue remain asymptomatic. This rate may be even lower in an adult population.

On 2017 May 05, Donald Forsdyke commented:

ORGANIC MEMORY

The view that Richard Semon's work was neglected seems to be based on psychologist Daniel Schacter's 1982 text (1). This was reissued with a new title and a few changes in 2001, without mention of the profound interim account by historian Laura Otis (2). While the authors cite my 2006 text on Samuel Butler and Ewald Hering, later work corroborates and extends Otis’s study and casts a somewhat different light on the authors' prime hero (3, 4).

Even if offering a list of heroes that is "entirely personal," a paper that extolls the "benefits of exploring the history of science" and of acknowledging our "debts … to those scientists who have offered key ideas," could have mentioned the doubts cast on Semon by Freud and Hertzog, and Semon's dismissal of Butler's work as "rather a retrogression than an advance."

1. Schacter DL (1982) Stranger behind the Engram: Theories of Memory and the Psychology of Science. Hillsdale, NJ: Erlbaum.

2. Otis L (1994) Organic Memory. History and the Body in the Late Nineteenth and Early Twentieth Centuries. Lincoln: University of Nebraska Press.

3. Forsdyke DR (2009) Samuel Butler and human long term memory: is the cupboard bare? J Theor Biol 258:156-164.Forsdyke DR, 2009

4. Forsdyke DR (2015) "A vehicle of symbols and nothing more." George Romanes, theory of mind, information, and Samuel Butler. History of Psychiatry 26:270-287. Forsdyke DR, 2015

On 2017 Sep 06, Tao Liu commented:

The webserver has moved to http://ccb1.bmi.ac.cn:81/htsrr/

On 2017 Oct 10, Kevin Hall commented:

This is a corrigendum to the original article (https://www.ncbi.nlm.nih.gov/pubmed/28074888) with the following correction:

Since the publication of the original article, the author has noticed that the references at the end of the third paragraph of the section ‘Experimental falsification of the carbohydrate–insulin model’ are incorrectly cited as 13, 14, where they should be 19, 20. The correction is given below:

‘In concordance with the model predictions, carbohydrate restriction led to increased fat oxidation reaching a maximum within a few days and remaining constant thereafter. However, neither study found the predicted augmentation of body fat loss with carbohydrate restriction. Rather, despite the reduction in insulin secretion, both studies found slightly less body fat loss during the carbohydrate restricted diets compared with isocaloric higher carbohydrate diets with identical protein.19,20’

However, for some strange reason, this published corrigendum goes on to incorrectly state the following:

The authors also noticed an error in reference 9. The correct reference is: Pahlavani N, Jafari M, Rezaei M, Rasad H, Sadeghi O, Rahdar HA, et al. L-arginine supplementation and risk factors of cardiovascular diseases in healthy men: a double-blind randomized clinical trial. F1000Res 2014; 3: 306. doi:10.12688/f1000research.5877.1.

The original reference 9 is actually correct and the author is mystified as to the source of this error.

On 2017 Jun 23, Alexander Kraev commented:

Regretfully, this article has a misleading title and abstract. The correct title should be "Strenuous exercise triggers a life-threatening response in C57BL/6J mice carrying RYR1 Y522S/WT and CASQ1 null mutations". Besides, the authors never care to state that they analyze the pathogenesis of an experimental disease, without attempting to decide, whether it is closely related to the respective disease of man.

On 2017 Jul 23, Giles Hardingham commented:

We would like to extend our sincere thanks to Michel Goedert for the use of his Thy1-P301S transgenic mouse (Allen et al. (2002), PMID: 12417659). Regrettably, this note was erroneously absent from the Acknowledgements section of the manuscript.

On 2017 May 09, Pavel Nesmiyanov commented:

Funny, but β-endorphin, oxytocin, and dopamine are not neuropeptides. They are not even peptides.

On 2017 Sep 18, Martine Crasnier-Mednansky commented:

The model for the chitin catabolic cascade indicates GlcNAc oligomers are degraded in the periplasm to ABC-transported (GlcNAc)2 and PTS-transported GlcNAc (figure 5 in Park JK, 2002 for the original model). The authors used (GlcNAc)4 and, because Enzyme IIA^Glc was largely phosphorylated in the presence of (GlcNAc)4, proposed there was "some mechanism for which chitin oligosaccharides escape from degradation into GlcNAc in the periplasmic space". If such mechanism occurs under the authors’ experimental conditions, it precludes any major PTS-transport effects on the chitin cascade, i.e. via dephosphorylation of Enzyme IIA^Glc during GlcNAc transport.

Working with Vibrio furnissii, Keyhani NO, 1996 argued, "since (GlcNAc)2 is an important inducer in the cascade, it must resist hydrolysis in the periplasm", and further provided an explanation for the stability of (GlcNAc)2 in the periplasm, particularly in sea water. It may well be that the rapid catabolism of (GlcNAc)2 is 'free' from any PTS control, and as such the cAMP necessary for the chitin cascade is provided.

On 2017 Jul 21, CO Stocco commented:

Thank you to the authors for such wonderful and detailed description of the extremely complex interaction between FSH and locally produced factors in the regulation of granulosa cells. This review will surely foster innovative ideas and projects to further explore the role of gonadotropins and growth factors in the regulation of female fertility.

On 2018 Feb 04, Sin Hang Lee commented:

The medical profession, including medical schools and hospitals, is now a part of the health care industry, and implementation of editorial policies of medical journals is commonly biased in favor of business interests. PubMed Commons has offered the only, albeit constrained, open forum to air dissenting research and opinions in science-based language. Discontinuation of PubMed Commons will silence any questioning of the industry-sponsored promotional publications indexed in PubMed.

On 2017 May 03, Sin Hang Lee commented:

In this Reply, Marks and colleagues did not dispute that 16S rRNA gene sequencing has provided objective evidence regarding the existence of chronic Lyme disease.

Marks and colleagues contended “persistent polymerase chain reaction (PCR) positivity for Borrelia burgdorferi does not signify the presence of active infection or bacteremia that merits prolonged antibiotic treatment.” However, neither PCR positivity, nor prolonged antibiotic treatment, was an issue raised in my Letter to Editor. The issue is: Does chronic Lyme disease exist? The answer is "yes". Whether bacteremia needs antibiotic treatment is beyond the scope of this discussion.

If a B burgdorferi 16S rRNA gene is detected in the DNA extraction of the pellet of the centrifuged serum or plasma sample from a patient, the positive test result serves to confirm that there were Lyme disease bacteria, dead or alive, circulating in the patient’s blood at the time when the blood sample was drawn – definition of bacteremia.Dead bacteria are quickly removed by the spleen and macrophages in other organs. Free foreign DNA in the blood of living mammals is known to be degraded or removed in 48 hours [1]. Many infectious diseases are diagnosed by testing the nucleic acid of the causative agents, for example the hepatitis C virus and the human papillomaviruses which are difficult to culture. Some of the bacterial strains causing Lyme borreliosis are not easily cultivated in artificial media. The references cited to dismiss the significance of gene sequencing in the diagnosis of Lyme disease are inappropriate.

Reference: [1] Schubbert R et al. Foreign (M13) DNA ingested by mice reaches peripheral leukocytes, spleen, and liver via the intestinal wall mucosa and can be covalently linked to mouse DNA. Proc. Natl. Acad. Sci. U. S. A. 1997; 94: 961-6.

Conflicts of Interest: Dr Lee is the director of Milford Molecular Diagnostics Laboratory specialized in developing DNA sequencing-based diagnostic tests.

On 2018 Feb 04, Sin Hang Lee commented:

The medical profession, including medical schools and hospitals, is now a part of the health care industry, and implementation of editorial policies of medical journals is commonly biased in favor of business interests. PubMed Commons has offered the only, albeit constrained, open forum to air dissenting research and opinions in science-based language. Discontinuation of PubMed Commons will silence any questioning of the industry-sponsored promotional publications indexed in PubMed.

On 2017 May 05, Sin Hang Lee commented:

In their Reply, Marks and colleagues did not dispute that 16S rRNA gene sequencing has provided objective evidence regarding the existence of chronic Lyme disease.

Marks and colleagues contended “persistent polymerase chain reaction (PCR) positivity for Borrelia burgdorferi does not signify the presence of active infection or bacteremia that merits prolonged antibiotic treatment.” However, neither PCR positivity, nor prolonged antibiotic treatment, was an issue raised in my Letter to Editor. The issue is: Does chronic Lyme disease exist? The answer is "yes". Whether bacteremia needs antibiotic treatment is beyond the scope of this discussion.

If a B burgdorferi 16S rRNA gene is detected in the DNA extraction of the pellet of the centrifuged serum or plasma sample from a patient, the positive test result serves to confirm that there were Lyme disease bacteria, dead or alive, circulating in the patient’s blood at the time when the blood sample was drawn – definition of bacteremia.Dead bacteria are quickly removed by the spleen and macrophages in other organs. Free foreign DNA in the blood of living mammals is known to be degraded or removed in 48 hours [1]. Many infectious diseases are diagnosed by testing the nucleic acid of the causative agents, for example the hepatitis C virus and the human papillomaviruses which are difficult to culture. Some of the bacterial strains causing Lyme borreliosis are not easily cultivated in artificial media. The references cited to dismiss the significance of gene sequencing in the diagnosis of Lyme disease are inappropriate.

Reference: [1] Schubbert R et al. Foreign (M13) DNA ingested by mice reaches peripheral leukocytes, spleen, and liver via the intestinal wall mucosa and can be covalently linked to mouse DNA. Proc. Natl. Acad. Sci. U. S. A. 1997; 94: 961-6.

Conflicts of Interest: Dr Lee is the director of Milford Molecular Diagnostics Laboratory specialized in developing DNA sequencing-based diagnostic tests.

On 2017 May 11, Alexis Frazier-Wood commented:

The key points section of this article, the purpose of which is to isolate the ‘key conclusion and implication based on the primary [study] finding(s)’, states that: “A randomized intervention that increased breastfeeding intensity was not associated with reduced obesity”. This is a selective interpretation of the study data on weight status, which show that maternal participation in the PROBIT intervention (which increased breastfeeding exclusivity and duration) was 1. associated with increased odds of offspring having adolescent overweight/obesity (odds ratio=1.14; 1.02-1.28) but 2. not associated having adolescent obesity (odds ratio=1.09; 0.92-1.29), although it can be seen that both associations were in the same direction. Body mass index (BMI) was also higher in the children from the intervention group by adolescence (mean difference Δ= 0.21, 0.06-0.36).

The reasons for the difference in significance (according to the specified alpha) between the results specifying BMI and overweight/obesity as outcomes vs. those specifying obesity likely arise from the differential power for the two outcomes. The relationship of breastfeeding to obesity vs. overweight/obesity had less power, largely due to the lower number of cases (obesity N=589 vs. overweight/obesity N=1868). Simulations in R v3.3.3, suggest the power for has “overweight/obesity” vs. has “obesity” was around 74% vs. 17%. These simulations did not account for the intention to treat procedure nor the correction for data clustering (since not enough data on e.g. ICC correlations was available), but due to the effects of these on power being equal across outcomes an assessment of relative power can be made. In addition, the alternative hypothesis (breastfeeding -> overweight/obesity) was formally tested, but the null hypothesis (breastfeeding ≠ obesity) was not, given the absence of any equivalence testing. Positive associations between breastfeeding and offspring adiposity have been reported before, but have not reached statistical significance (see Cope MB, 2008). Therefore, while the association of increased breastfeeding with significantly increased odds of overweight/obesity represents a novel finding which needs to be subjected to replication, without recourse to empirically stronger results, omitting this from the overall interpretation of the study in favor of a lesser powered, untested hypothesis represents a form of bias.

While the manifestation of bias in the article may be small, its effect can still be pernicious. Several organizations, including the World Health Organization and the American Heart Association, state that breastfeeding provides protection against offspring obesity (see WHO report and AHA Fact Sheets). However, this lacks strong statistical justification, given that any inverse associations between breastfeeding and offspring obesity are derived from observational designs and likely to reflect confounding (Kramer MS, 2002), and that probability theory suggests that the breastfeeding-offspring obesity data in the literature as a whole reflect one of two situations: (1) publication bias, or (2) a true positive association between breastfeeding and offspring obesity in at least one other published sample (Cope MB, 2008). That is not to deny that there may be a number of valid reasons to support breastfeeding, not related to obesity (see e.g. APA report). But perhaps it is this which has lead to a problem with ‘white hat bias’ in the breastfeeding-obesity literature - a term coined by Cope and Allison to denote ‘bias leading to the distortion of research based-based information in the service of what may be perceived as righteous ends (Cope MB, 2010). One such reason to support breastfeeding is to enable personal choice for parents and caregivers. However, this is incompatible with the practice of giving misleading information on the benefits of breastfeeding which actually deprives caregivers of their right to make informed decisions about feeding infants.

This is a problematic situation, and needs to be corrected. The causes are unknown, but distorted presentation of data has been identified in multiple reports of randomized clinical trials, often in only one section e.g. the abstract (Boutron I, 2010), and often in the secondary literature, such as press releases (Cope MB, 2010). Therefore all authors need express conclusions with great clarity and consistency, and not selectively include and exclude results without recourse to relative empirical strengths. To be accurate in reporting in this article, the results of this study as a whole are most consistent with either (1) an association between breastfeeding and increased offspring overweight/obesity, or (2) a lack of empirical strength in this study to contribute to the debate on whether there is an association between the two constructs.

On 2017 Aug 15, Varshil Mehta commented:

Great work. Congrats to the authors.

On 2017 May 08, Ellis Muggleton commented:

HEp2 Cells are HeLa cells, not laryngeal cancer cells.

On 2017 May 13, Annie De Groot MD commented:

The author GROOT is actually De Groot. See De Groot, AS in pubmed.

On 2017 May 03, Kenneth Pollard commented:

Last author should be Pollard KM.

Author affiliation for last author should be 5 Department of Molecular Medicine, The Scripps Research Institute, La Jolla, CA, USA 92037. mpollard@scripps.edu.

On 2017 May 07, Clive Bates commented:

Has it occurred to the authors that the value (or 'USP') of new and emerging tobacco or nicotine product like e-cigarettes or heated tobacco products might be that they really are very much "better and safer" than smoking?

No serious scientist doubts this. The question is by how much, with many credible sources suggesting 95% or greater reduced risk (see, for example, the Royal College of Physicians' 2016 report Nicotine without smoke: tobacco harm reduction).

However, the authors' conclusion appears to be inviting regulators to mislead the public about the risks of these products in order to reduce demand for them. There are many problems with such an approach:

• It is ethically improper for the state to intervene in this way to manipulate adult choices by withholding or distorting information (see: Kozlowski LT, 2016).<br>
• The unintended, but wholly foreseeable, effect of trying to prevent people using safer alternatives to cigarettes is not that they quit smoking, but that they carry on smoking - and are harmed as a result of regulatory misinformation.
• How would regulators (or the authors) take responsibility and assume liability for harms arising from deceptive communications that adversely influence behaviour?
• Companies have a right to make true and non-misleading statements about their products. Under what principle should they be prevented from doing that?

The appropriate approach for a regulator is to truthfully inform smokers of the relative risks of different nicotine products. That would allow consumers to make informed choices that could prevent disease, save life and improve welfare. It is not to enforce abstinence from the use of the legal drug nicotine, which in itself, and without delivery through tobacco smoke, poses low risks to health.

Once again, tobacco control academics proceed from results to conclusions and on to policy prescription without any remotely adequate policy evaluation framework or any apparent awareness of the limitations of their analysis.

On 2017 Apr 29, Ellen M Goudsmit commented:

I am concerned that two previous efforts to correct factual errors have not been incorporated in the revision.

1. I have previously written to the main author that Wallman et al evaluated pacing, as defined by Goudsmit et al (2012). This is very different from the GET protocols used in other RCTs. I suspect that few readers would be aware of the difference between GET and pacing.<br>
2. No study assessing GET used the original or revised London criteria for classic ME (Goudsmit et al 2009). The version published by the Westcare ME Task Force is different from both as well as incomplete. Research has indicated that the Westcare ME criteria select a different sample (Jason et al, personal communication). As no study has yet assessed exercise for classic ME, one can not generalise any conclusion about efficacy from the trials in the review to patients with this disease.
3. As pointed out by Professor Jason who devised the Envelope theory, Adaptive Pacing Therapy (APT) is not based on the former. Again, this has been pointed out before.
4. APT should not be equated with the strategy of pacing recommended by many self-help groups. Pacing helps (cf. all surveys conducted to date): APT is of little value (White et al, 2011). NB: The PACE trial did not assess pacing.

Science demands precision so I hope that this third attempt to correct errors will be responded to in an appropriate manner. To repeat inaccurate information undermines the scientific process.

Goudsmit EM, Jason LA, Nijs J, et al. (2012) Pacing as a strategy to improve energy management in myalgic encephalomyelitis/chronic fatigue syndrome: A consensus document. Disability and Rehabilitation 34(13): 1140-1147.

Goudsmit EM, Shepherd C, Dancey CP, et al. (2009) ME: Chronic fatigue syndrome or a distinct clinical entity? Health Psychology Update 18(1): 26-33. Available at: http://shop.bps.org.uk/publications/publications-by-subject/health/health-psychology-update-vol-18-no-1-2009.html

Jason LA (2017) The PACE trial missteps on pacing and patient selection. Journal of Health Psychology. Epub ahead of print 1 February.

Jason LA, Brown M, Brown A, et al. (2013) Energy conservation/envelope theory interventions. Fatigue: Biomedicine, Health & Behavior 1(1-2): 27-42.

ME Association (2015) ME/CFS Illness management survey results. ‘No decisions about me without me’. Part 1. Available at: http://www.meassociation.org.uk/wp-content/uploads/2015-ME-Association-Illness-Management-Report-No-decisions-about-me-without-me-30.05.15.pdf (Various survey results in Appendix 6)

White PD, Goldsmith KA, Johnson AL, et al. (2011) PACE trial management group. Comparison of adaptive pacing therapy, cognitive behaviour therapy, graded exercise therapy, and specialist medical care for chronic fatigue syndrome (PACE): A randomised trial. The Lancet 377: 823–836.

On 2017 Nov 28, Andrea Messori commented:

Ventral hernia surgery: economic information in a series of Italian patients

Andrea Messori, Sabrina Trippoli

HTA Unit, ESTAR Toscana, Firenze, Italy

The paper by Rampado et al. [1] is the first analysis that examines the issue of costs in Italian patients undergoing incisional hernia repair with synthetic or biological meshes. One interesting finding of this study is the analysis of DRGs and reimbursements observed in this real-life setting. Table 2 of the article by Rampado et al. [1] shows that 7 different DRGs were employed for the overall series of 76 patients divided in three groups. The amounts reimbursed according to these 7 DRGs ranged from EUR 1,704.03 to EUR 13,352.72 (mean value = EUR 2,901 weighted according to the number of patients in the three groups). The length of stay was more homogenous across the three groups (7 days in Group 1, N=35; 7 days in Group 2, N=31; 13 days in Group 3, N=11), with a mean value of 7.87 days weighted according to the size of the three groups. According to Rampado et al.[1], DRGs in Italy are an underestimation of real costs. In fact, while the weighted mean of reimbursements is EUR 2,901, the weighted mean for cost in the same patients is EUR 6,908. This real-life information on costs can be extremely useful for conducting modeling studies that evaluate the cost effectiveness of meshes in Italian patients subjected to incisional hernia repair with synthetic or biological meshes.

References

1. Rampado S, Geron A, Pirozzolo G, Ganss A, Pizzolato E, Bardini R. Cost analysis of incisional hernia repair with synthetic mesh and biological mesh: an Italian study. Updates Surg. 2017 Sep;69(3):375-381. doi:10.1007/s13304-017-0453-9.

On 2017 Apr 28, Gabriel Lima-Oliveira commented:

"Brazilian scientific societies currently allow laboratory directors choose between fasting/no-fasting time for all laboratory tests when prescribed together with lipid profile; but such a ‘‘permit’’ is not granted by any scientific evidence. Fasting time for most blood tests should be 12 hours, whereas for lipid profile alone is an exception based on European consensus."

Text published by Journal of Clinical Lipidology Official Journal of National Lipid Association. All rights reserved

On 2017 Jul 13, David Nunan commented:

On the day this editorial was released we contacted the Editor for consideration of the following commentary. We have yet to hear back from the Editor. To avoid further delay via formal submission, we present here a truncated version of our commentary.

Response to “Saturated fat does not clog the arteries: coronary heart disease is a chronic inflammatory condition, the risk of which can be effectively reduced from healthy lifestyle interventions”

Implausible discussions in saturated fat “research”

Definitive solutions won’t come from another million editorials (or a million views of one).

The British Journal of Sports Medicine again acts as the unusual home to an opinion editorial advocating for public health guidance on saturated fat to be revised based on selected “evidence”. As an editorial it was always going to struggle to avoid calls of “cherry picking”. More worrying was the failure to apply even the basic of evidence-based principles. Here, we do the job of authors (and editor[s]) in addressing the quality of the evidence presented and highlighting some of the contradictory evidence, the complexity and uncertainty of the evidence-base whilst being mindful of our own cognitive biases.

Effects of reducing saturated fat intake for cardiovascular disease

The authors refer to evidence from a “landmark” meta-analysis of observational studies to show a lack of an association between saturated fat consumption and all-cause mortality, coronary artery disease incidence and mortality, ischaemic stroke, and type 2 diabetes [1]. According to best practice evidence-based methods, the types of studies included here provide low quality evidence (unless specific criterion are met) [2]. Indeed, the review authors actually reported the certainty of reported associations (or lack there of) was “very low”, indicating any estimates of the effect are very uncertain [1].

Conversely, a high-quality meta-analysis of available RCTs (n= 17 with ~59,000 participants) from the Cochrane Collaboration, found moderate quality evidence from long-term trials that reducing dietary saturated fat lowered the risk of cardiovascular events (number needed to treat [NNT]=14), but no effect on all-cause and cardiovascular mortality, risk of myocardial infarction, and stroke, compared to usual diet [3]. The Cochrane review also found in subgroup analyses, the reduction in cardiovascular events was observed in the studies replacing saturated fat with polyunsaturated fat (but not with carbohydrates, protein, or monounsaturated fat).

Thus the consensus viewpoint of a beneficial effect of reduced dietary saturated fat and replacement with polyunsaturated fat in the general population appears to be underpinned by a higher quality evidence base.

Benefits of a Mediterranean diet on primary and secondary cardiovascular disease

In the section “dietary RCTs with outcome benefit in primary and secondary prevention”, the authors switch from saturated fat to low fat diets and cite two trials, namely the PREDIMED study [5] and the Lyon Diet Heart study [6].

The PREDIMED study investigated the effects of a Mediterranean diet including fish, whole grain cereals, fruits and supplemented with extra-virgin olive oil versus the same Mediterranean diet supplemented with mixed nuts, versus advice to reduce dietary fat on primary prevention of cardiovascular disease. The dietary interventions in PREDIMED were designed to increase intakes of mono- and poly-unsaturated fat and reduce intake of saturated fat.

The Lyon Diet Heart study examined the impact of a Mediterranean alpha-linolenic acid-rich (with significantly less lipids, saturated fat, cholesterol, and linoleic acid) compared to no dietary advice. This study also aimed to assess the effect of increase dietary intake of unsaturated (polyunsaturated) fats.

Both these studies support the current consensus to increase intakes of polyunsaturated dietary fats in replacement of saturated fat. These findings also suggest placing a limit on the percentage of calories from unsaturated fats may be unwarranted which has now been acknowledged in a recent consensus [7].

Furthermore, a meta-analysis reviewing the effects of the Mediterranean diet on vascular disease and mortality [8], found that using the best available data the Mediterranean diet reduced vascular events and incidence of stroke, but did not result in improvements in all-cause mortality, cardiovascular mortality, coronary events, or heart failure compared to controls. The review authors highlighted the limited quantity and quality of evidence and the uncertainty of the effects of a Mediterranean diet on cardiovascular outcomes, and the non-existence of data about adverse outcomes.

LDL-Cholesterol and Cardiovascular mortality

The authors support their view that the cardiovascular risk of LDL-cholesterol has been exaggerated with 45 year-old data from the Minnesota Coronary Experiment (MCE) [9] and a systematic review of observational studies [10]. However, the authors do not address observed limitations of the MCE study including discrepant event rate and selective outcome reporting, over 80% attrition (with lack of intention-to-treat analysis and a small event rate difference (n=21) plausibly driven by a higher unexplained drop out in the control group [11].

The review cited found that LDL-cholesterol is not associated with cardiovascular disease and is inversely associated with all-cause mortality in elderly populations [10]. However, the methodological quality of this review has been judged to be poor for, among other problems, non-uniform application of inclusion/exclusion criteria, a lack of critical appraisal of the methods used in the eligible studies (low quality observational studies), failure to account for multifactorial analysis (i.e., lack of control for confounders), and not considering statin use (see Eatz letter in response to [12] and [13]).

The authors fail to discuss large-scale RCT evidence showing that LDL-cholesterol reducing statin therapy reduces the risk of coronary deaths, myocardial infarction, strokes, coronary revascularisation procedures by ~25% for each mmol/L reduction in LDL-cholesterol during each year, following the first, it is taken [14]. We are aware of the on-going debate around the integrity of the data in relation to statins, particularly around associated harms, and their potential mechanisms. However, there appears general consensus on their effectiveness in reducing hard endpoints regardless of their underlying mechanism.

Therefore, given the flaws of the referenced trial and systematic review of observational studies and evidence in support of benefits of LDL-cholesterol lowering therapy, it is too early to dismiss LDL-cholesterol as a risk factor for cardiovascular disease and mortality.

We note with interest the authors’ statement “There is no business model or market to help spread this simple yet powerful intervention.” It’s not beyond comprehension that journals present a credible business model based on attracting controversy in areas of public health importance where clarity, not confusion, is needed. Notable conflicts of interest include income from a low budget film purporting the benefits of a high saturated fat diet.

The latest opinion editorial overlooks a large contradictory evidence-base and the inherent uncertainty with nutritional epidemiological studies and trials [15]. Arguably what is needed is a balanced discussion of dietary patterns over and above individual macronutrients that considers collaborative efforts for improving the evidence-base and our understanding of the complex relationship between dietary fat and health.

References available from corresponding author.

David Nunan^1*, Ian Lahart^2. ^1Senior Researcher, University of Oxford, UK. david.nunan@phc.ox.ac.uk *Corresponding author ^2Senior Lecturer in Exercise Physiology, University of Wolverhampton, UK

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 Sep 12, Rima Obeid commented:

Trimethylamine N-oxide and platelets aggregation: insufficient evidence for causal inference in thrombosis - http://amj.amegroups.com/article/view/4016/4744

Trimethylamine N-oxide (TMAO) is an amine oxide generated in the liver from nutrients such as choline, betaine, or carnitine via an intermediate gut-bacteria driven metabolite, trimethylamine (TMA). Recently, Zhu et al. conducted a 2-month open-, non-placebo controlled intervention in vegetarians and omnivores using 450 mg total choline/day (1). Zhu et al. reported a significant increase in plasma TMAO concentrations (from 2.5 to 36.4 microM in omnivores and from 2.6 to 27.2 microM in vegetarians). A corresponding increase in platelet aggregation according to an in vitro platelets function test was also reported and expressed as percentage of maximal amplitude. The assumed effects of TMAO on platelets aggregation were observed at the first follow-up visit, 1 month after the start of supplementation, and the effects were stronger in omnivores compared with vegetarians (1). No further changes occurred in the following month of supplementation. There is no information on latency period, sustainability of the effect, or resistance to high TMAO levels. The results suggest that the increase in platelet aggregation have leveled off after 1 month (no further increase between month 1 and month 2). There is no evidence on sustainability of the effect after the last oral choline dose that was taken in the evening before the platelet function test. The results of the adenosine diphosphate (ADP)-induced platelets aggregation in vitro were interpreted as prothrombotic effect of TMAO (1). After aspirin usage in subjects without platelets disorders, lowering of in vitro platelets-reactivity to 5 microM ADP was hypothesized to indicate that “TMAO may overcome antiplatelet effects of aspirin”. Nevertheless, the interactive effect of aspirin and TMAO can be equally argued to indicate that: “TMAO may reduce the risk of bleeding from aspirin” or “TMAO may reduce resistance to aspirin in subjects who need anti-platelet drugs”. But how to interpret the results in term of cause and effect?

Platelet aggregation is a highly complex process involving numerous cellular receptors and transmembrane pathways. Platelet activation occurs when agonists, such as ADP, thromboxane A2 (TxA2), and thrombin, bind to their receptors. This physiological process is involved in protective hemostasis (i.e., prevents bleeding by forming cloth) as well as in pathological thrombosis (over-aggregation). A variety of agonists such as ADP, epinephrine, arachidonic acid, or collagen can induce platelet aggregations via different mechanisms (2). This characteristic has been used for in-vitro diagnosis of platelet disorders and for monitoring resistance to anti-platelets. Nevertheless, assays that use a single agonist or a single concentration of any agonist are oversimplification of platelet function that could be completely different under physiological conditions (3).

In vivo platelets activation causes ADP to release from dense granules. ADP activates surface glycoprotein IIb/IIIa that is attached to fibrinogen, thus leading to aggregation of platelets to adherent layer. Adding ADP to platelets rich plasma (in vitro) causes an initial increase in aggregation due to activation of the glycoprotein IIb/IIIa platelets membrane receptor and a second wave of aggregation due to recruitment of additional platelets aggregates. In contrast, aspirin inhibits platelet activation mainly by targeting cyclooxygenase 1 (COX-1) thus leading to inhibition of TxA2 formation. Because arachidonic acid affects the COX-1/TxA2 system, this compound is used, instead of ADP, for in vitro induction of platelets aggregation in platelet rich plasma under aspirin treatment. Despite that aspirin has been shown to reduce platelet aggregation induced by ADP, aspirin inhibition of platelets aggregation after arachidonic acid is greater and this test is used for routine monitoring of aspirin effect (4,5).

Zhu et al. observed higher platelet aggregation at high TMAO (compared with low TMAO) and lower aggregation under aspirin compared with the same subject without aspirin (1). The results are not interpretable for the following reasons; first, because the results of the platelets aggregation in platelets rich plasma are not comparable between studies, agonists, and agonists concentrations (6); second, because TMAO was anticipated to inhibit surface glycoprotein IIb/IIIa (that is activated by ADP), but aspirin acts mainly via TxA2. Thus, using ADP as an agonist for the surrogate platelet aggregation test is not selective for aspirin effect. However, what would have happened in subjects with indication for anti-platelets treatment? Could high TMAO be protective against bleeding? Could it reduce resistance to long term antiplatelet therapy? Could there be a platelet-adaptation to high choline intake? Clearly these questions are not answered yet.

The long-term risk of thrombosis associated with high choline intake or high plasma TMAO is not evident. The value of platelet function tests in predicting future thrombosis in non-symptomatic individuals has been questioned by the Framingham Heart Study cohort where no association was found between several platelets function tests (including ADP-aggregation) and future thrombosis after controlling for other likely competing risk factors (6). Similar negative results were reported by Weber et al., who found that ADP-aggregation was not associated with thrombosis (7). Moreover, compared with omnivores, vegetarians could have fewer or larger platelets. In addition, any possible association between TMAO and platelet functions could be subject to effect modification from dietary components such as betaine, carnitine, fatty acids, lipids, or micronutrients (8,9). In line with this, Zhu et al. have indeed shown that the platelet aggregation results that were not different between vegetarians and omnivores at baseline, became different after 1 and 2 months of supplementation of 450 mg/day choline. Therefore, since the intervention was identical in both groups, the results strongly suggest the presence of effect modifications via yet unknown factors.

Zhu et al. have shown that aspirin lowers plasma TMAO after choline load by almost 50% within 1 month (1). This could be related to changing gastrointestinal acidity and bacterial populations, thus affecting the production rate of TMA; affecting FMO3 system; or affecting a yet unknown TMA-metabolizing system. The results also draw attention to the role of aspirin (and possibly many other drugs) as an effect modifier in clinical studies on the role of TMAO in vascular diseases.

If the study of Zhu et al. (1) is to be used for synthesizing evidence, the following arguments can be made: the hypothesis could be “exposure to TMAO causes thrombosis (shown by using an appropriate surrogate test)” (Figure 1). A randomized controlled trial would be an appropriate design. However, dietary intakes of other sources of TMAO should be controlled and confounding from aspirin or other well-known factors (i.e., renal dysfunction, inflammation, or vascular diseases) that affect TMAO and simultaneously the outcome “platelet aggregation” should be conditioned on. Information on short and long term effects of high choline intake is equally important because of platelet adaptation and analytical limitations of most available surrogate in vitro tests. Since the effect does not appear to further increase over time, resistance or adaptation to high TMAO could be equally a valid explanation.

Taken together, because of serious limitations in the study design, inappropriate surrogate outcomes, unknown kinetics of the response of platelets to TMAO, and uncontrolled confounders there is a risk of using such data for causal inference on a proposed direct prothrombotic effect of dietary choline.

On 2017 May 13, David Keller commented:

Low LDL cholesterol was associated with significantly higher risk of Parkinson disease than was high LDL

The authors report that the adjusted hazard ratio for Parkinson disease ("PD") in subjects with LDL < 1.8 mmol/L versus those with LDL >4.0 mmol/L was 1.70 [1.03 - 2.79]. Note that the 95% confidence interval (in brackets) does not cross 1.0, so this association of low LDL with increased risk of PD is statistically significant.

The above data were then subjected to "genetic, causal analysis", which yielded a risk ratio for a lifelong 1 mmol/L lower LDL cholesterol level of 1.02 [0.26 - 4.00] for Parkinson's disease. Note that the 95% confidence crosses 1.0, and the mean risk ratio of 1.02 is barely elevated.

The tiny and non-significant increase in PD risk caused by a lifelong 1 mmol/L lower serum LDL level, as calculated by the genetic causal analysis, appears to contradict the significant increase in risk of PD for subjects with LDL < 1.8 mmol/L, as compared with subjects with LDL > 4.0 mmol/L seen in the observational analysis.

This apparent contradiction may be an artifact of the diminished statistical power of the genetic causal analysis (which compared change in PD risk for a change in LDL of only 1 mmol/L) versus the observational study, which found significantly higher PD risk associated with LDL < 1.8 mmol/L than with LDL > 4.0 mmol/L. In the observational analysis, the LDL in the high-PD-risk subjects was at least 2.2 mmol/L lower than in the low-risk subjects (ie: 4.0 - 1.8 = 2.2 mmol/L). Thus, the genetic causal analysis calculated the effect of an LDL lower by only 1.0 mmol/L, while the observational analysis looked at the effect of an LDL lower by at least 2.2 mmol/L.

I suggest that the authors compare apples with apples, by re-calculating the genetic, causal analysis to determine the effect of lifelong lowering of LDL by at least 2.2 mmol/L, the minimum separation of LDL levels between subjects in the comparator groups in the observational analysis. Comparing the effect of a larger decrease in LDL may enhance the size and significance of the results calculated by the genetic analysis, and bring it into agreement with the significantly increased risk of lower LDL found in the observational analysis.

On 2017 Apr 26, Zhang Weihua commented:

Congratulations! Great work! Thanks for citing our paper!

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

It is time to rethink about our experimental models for cancer study.

On 2017 Oct 24, Jim van Os commented:

We would like to report two small and non-essential errors in the publication of this paper:

1. The first error is in Table 2, page 6: The bottom row in the column of mean PRS values, now depicted as ‘-0.28’ with a standard deviation of ‘0.55’ is incorrect and has to be replaced by ‘0.77’ with S.D = ‘0.19’.

2. The second error pertains to the text in the results section on page 5, the fifth paragraph under the heading ‘Associations in relatives and healthy comparison subjects’ in which the results of associations between PRS and CASH-based lifetime depressive and manic episodes are reported. The results of OR’s, CI’s and p-values for the outcome of ‘any affective episode’ in both the relatives group and the healthy comparison group in this text have to be replaced with the corresponding OR;s, CI’s and p-values reported in Table 7, page 11 for any affective episode.

On 2017 Apr 22, Alessandro Rasman commented:

Aldo Bruno MD, Pietro M. Bavera MD, Aldo d'Alessandro MD, Giampiero Avruscio MD, Pietro Cecconi MD, Massimiliano Farina MD, Raffaello Pagani MD, Pierluigi Stimamiglio MD, Arnaldo Toffon MD and Alessandro Rasman

We read with interest this study by Zakaria et al. titled "Failure of the vascular hypothesis of multiple sclerosis in a rat model of chronic cerebrospinal venous insufficiency".(1) Unfortunately the authors ligated the external jugular veins of the rats and not the internal jugular veins. Dr, Zamboni's theory on chronic cerebrospinal venous insufficiency is based on the internal jugular veins and not on external jugular veins.(2) Maybe the authors can read the two papers from Dr. Mancini et al. (3) and (4). So, in our opinion the title of this study is absolutely not correct.

References: 1. Zakaria, Maha MA, et al. "Failure of the vascular hypothesis of multiple sclerosis in a rat model of chronic cerebrospinal venous insufficiency." Folia Neuropathologica 55.1 (2017): 49-59. 2. Zamboni, Paolo, et al. "Chronic cerebrospinal venous insufficiency in patients with multiple sclerosis." Journal of Neurology, Neurosurgery & Psychiatry 80.4 (2009): 392-399. 3. Mancini, Marcello, et al. "Head and neck veins of the mouse. A magnetic resonance, micro computed tomography and high frequency color Doppler ultrasound study." PloS one 10.6 (2015): e0129912. 4. Auletta, Luigi, et al. "Feasibility and safety of two surgical techniques for the development of an animal model of jugular vein occlusion." Experimental Biology and Medicine 242.1 (2017): 22-28.

On 2017 May 12, Lydia Maniatis commented:

"The high levels of correlation between the four measures used in this study (fixations, interest points, taps and computed salience; see Fig. 3) support the conclusion that the tapping paradigm is a valid measure of salience."

Ascertaining that people look where they point (how could they guide their movement if they didn't?) has to be very high on the list of predictable predictions. With respect to "computed salience,": "Finally, saliency maps computed from the Itti et al. (1998) model were compared against the tap data and found to correlate beyond the null hypothesis, Rӻ bTޠ젰:21; p 젴:3 1015, though not significantly below the sample error hypothesis, Rӻ eST ޠ젰:25; p 젰:075. This relatively low value of Rӻ eST ޠis obtained because the computed saliency maps were relatively diffuse."

"In the absence of a specific task (蘦ree viewing� it seems reasonable to assume that at least for the first few images, and for the first few fixations in these images, observers let themselves be guided by the visual input, rather than by some more complex strategy..."

The criterion of "it seems reasonable [to us] to assume that..." is the contemporary definition of rigor (providing a solid rationale or even testing assumptions, in this case at the least debriefing subjects). In contrast, it seems reasonable to me to assume that if someone asks me to freely select a place in a picture to point to, I would want to point at something interesting or meaningful, not at the first thing that caught my attention, e.g. the brightest spot. That is, observers awareness that someone else is observing and in some way assessing their choices makes the authors assumptions that they are limiting "top-down" influences seem very weak to me. Of course, the top-down/bottom up distinction is itself completely vague. If, in the image, I see two chairs and a sofa and point to the one that I immediately recognize as having seen in IKEA, is this top-down or bottom up?

Relatedly, the authors casually address the issue of how many fixations preceded the pointing during the 1.4 seconds of viewing time: "Note that for the tapping study, the reaction time includes the time after the subject has decided where to tap, the movement of the hand, as well as the (relatively short) delay between the tap on the initialization screen and the presentation of the image. We therefore estimate that the majority of subjects performed three or fewer saccades before deciding where to tap." So, at least 127/252? Is this really an adequate assumption? And what is the rationale for 촨ree or fewer�eing an important cut-off?

It's also typical of the contemporary approach that the experimental emphasis is wholly on technique and statistics and completely agnostic to the actual stimuli/conditions and to the percepts to which they give rise, as well as to the many fundamental conceptual issues that such considerations entail, and of course the effect of stimulus variations on the shape of the data.

This empirical agnosticism is reflected in the use of the term "natural scene" to characterize stimuli; it is completely uninformative as to the characteristics of the stimuli. (This is especially the case as "natural scene" here includes, as it often does in scholarly publications, images of buildings on a college campus).

Surely, certain sets of such stimuli would produce greater or smaller inter-individual differences than others, altering the already weak data significantly as to "saliency maps." For example, if an image contained one person, then attention would generally fall on this person. But if there were two people, the outcome would probably be divided between the two, and so on. (Is seeing a person in a brief presentation top-down or bottom-up?)

Wouldn't it be weird if "attentive pointing" DIDN'T correlate with "other measures of attention"? So weird that the interpretation of the results would probably be chalked up to the many sampling uncertainties and confounding factors that are, in the predictable case, bustled through with lots of convenient (or "reasonable") assumptions and special pleading for weak data.

On 2017 May 01, Lydia Maniatis commented:

Like too many in the vision literature, this article recycles various unviable odds and ends from the theoretical attic. The general discussion begins with this amazing statement: “It is generally accepted that lateral inhibition among orientation-selective units is responsible for the tilt illusion.” The collection of citations mentioned in the subsequent discussion provides absolutely no support for this completely untenable (if somewhat ambiguous) statement, as all they show is that the perception of any element in the visual field is affected by the structure of the surrounding field. Perhaps (no guarantee) the cases cited could superficially be reconciled with the "lateral inhibition" claim; but it crashes and burns in an infinite number of other cases, the perception of orientation being wholly contingent on a sophisticated structural interpretation of the retinal stimulation; and the neurons responsible for this interpretive activity are, of course, the same neurons supposedly acting via dumb (so to speak) local interactions to produce the "tilt illusion."

The claim that neurons act as detectors of orientation, each attuned to a particular value, is equally untenable (as Teller (1984) has pointed out in detail). Again, claims such as : “lateral interactions between these lines, or neurons, can skew the distribution and change the perceived orientation” are blind to the fact that perception does not act from local to global, but is effectively constrained by the whole visual field and the values inherent in the possible organizations of this field, which are infinite and among which it generally "chooses" only one. We don’t see the tilt of the lines composing the drawn Necker cube veridically from a 2D point of view; so if there were “labeled lines” for tilt, as the authors suggest, then these responses cannot directly affect the percept; but direct percepts are what the authors are using to draw their conclusions. Also, an orientation is a feature of a structure; and any structures in perception are constructed, along with their orientation, from point stimulation from photons striking the retina; so this is a case of the visual system supposedly "detecting" features of things that it has itself created.

Similarly: “Known psychophysical features of the tilt illusion … also suggest low-level locus of the tilt illusion. Taken together, V1 is a likely locus for the main site of the tilt illusion.“ The attribution of perceptual experiences to ‘low level’ or peripheral cortical processes was also criticized by Teller (1984) who noted that it implicitly relies on a “nothing mucks it up” proviso, i.e. assuming the low level activity is directly reflected in the percept, without explaining what happens upstream. Again, attributing a perceptual effect such as the perceived tilt of an image to simple interactions in the same V1 neurons that are responsible for observers' perception of e.g. forms of the room, the computer, the investigators, the keypad, etc., is not credible. It would be paradoxical to claim, as Graham (1992) has done, that some percepts are a direct, conscious reflection of low level neural activity, as there would have to be a higher level process deciding that the interpretation of image x should be mediated only by the lower level, and the products shunted directly to consciousness. Such arguments should never be made again.

Similarly: “To summarize, spatial contextual modulations of V1 neurons and their population responses seem to be likely candidates for the neural basis for simultaneous hue contrast.”

The references to “simultaneous contrast mechanisms” is inapt for all the same reasons, i.e. that this is a an effect highly sensitive to global context with sophisticated criteria, and thus cannot be simply segregated theoretically from the processes of perceptual organization in general.

Finally, I don't get this: "No fixation point was provided..." but then "The observers' task was to adjust the orientation of the comparison grating, which was presented on the other side of the fixation point…” Was there or wasn't there?

On 2017 Jun 07, Michelle Fiander commented:

PRISMA describes elements to report; not how to conduct a systematic review. THe Newcastle/Ottawa score is appropriate for non-RCT but not for RCTs. Of the 2 RCTs included in this review, Rezk 2016, for example, may not have scored as high on Cochrane RoB as on the Newcastle scale.

On 2017 Oct 31, Lise Bankir commented:

About osmoles and osmolytes

It is important to use the right words to ensure an unambiguous understanding of the diverse aspects of scientific studies. Thus, I would like to draw attention to the difference between "osmolytes" and "osmoles".

The word "osmolyte" is misused in this paper and should be replaced throughout by "osmole".

Osmoles (e.g. sodium, potassium, chloride, urea, glucose) are substances that increase the osmolarity of the fluid in which they are dissolved.<br> Osmolytes (e.g. betaine, sorbitol, myoinositol, glycine, taurine, methyamines) are substances that accumulate inside cells to protect them from a high ambient osmolarity.

See definition of osmolytes in the two encyclopedia below.

http://www.encyclopedia.com/science/dictionaries-thesauruses-pictures-and-press-releases/osmolyte

https://en.wiktionary.org/wiki/osmolyte

See also reviews about osmolytes (two examples given below).

J Exp Biol. 2005 Aug;208(Pt 15):2819-30. Organic osmolytes as compatible, metabolic and counteracting cytoprotectants in high osmolarity and other stresses. Yancey PH

Curr Opin Nephrol Hypertens. 1997 Sep;6(5):430-3. Renal osmoregulatory transport of compatible organic osmolytes. Burg MB

On 2017 Aug 28, NephJC - Nephrology Journal Club commented:

The controversial and thought-provoking paper “Increased salt consumption induces body water conservation and decreases fluid intake.” was discussed on June 6th and 7th 2017 on #NephJC, the open online nephrology journal club.

Introductory comments written by Joel Topf are available at the NephJC website here

181 people participated in the discussion with nearly 1000 tweets. We were delighted that Paul Welling, an expert in renal physiology also joined in the chat.

The highlights of the tweetchat were:

• Nephrologists were surprised that the ‘basic tenet’ of Nephrology that is steady state sodium balance is now in dispute.

• The methodology of this study was very impressive with the simulated Mars missions Mars105 and Mars 520 providing a unique opportunity to do prolonged metabolic balance studies, albeit in only 10 subjects.

• It was unclear if the salt content was blinded or not and this may limit result interpretation.

• It’s interesting that cortisol may have a more important role in sodium/water balance than previously thought via its stimulation of protein catabolism to generate more urea for urine concentration, however its overall significance is still thought to be considerably less than that of ADH/aldosterone.

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 Oct 31, Lise Bankir commented:

About osmoles and osmolytes

It is important to use the right words to ensure an unambiguous understanding of the diverse aspects of scientific studies. Thus, I would like to draw attention to the difference between "osmolytes" and "osmoles".

The word "osmolytes" is misused in this paper and should be replaced throughout by "osmoles".

Osmoles (e.g. sodium, potassium, chloride, urea, glucose) are substances that increase the osmolarity of the fluid in which they are dissolved.<br> Osmolytes (e.g. betaine, sorbitol, myoinositol, glycine, taurine, methyamines) are substances that accumulate inside cells to protect them from a high ambient osmolarity.

See definition of osmolyte in the two encyclopedia below.

http://www.encyclopedia.com/science/dictionaries-thesauruses-pictures-and-press-releases/osmolyte

https://en.wiktionary.org/wiki/osmolyte

See also reviews about osmolytes (two examples given below).

J Exp Biol. 2005 Aug;208(Pt 15):2819-30. Organic osmolytes as compatible, metabolic and counteracting cytoprotectants in high osmolarity and other stresses. Yancey PH

Curr Opin Nephrol Hypertens. 1997 Sep;6(5):430-3. Renal osmoregulatory transport of compatible organic osmolytes. Burg MB

On 2017 Oct 31, Lise Bankir commented:

See E-Letter to the JCI Editor about this article, by Richard Sterns and Lise Bankir

"Of Salt and Water: Let's Keep it Simple"

https://www.jci.org/eletters/view/88532#sec1

On 2017 May 06, Christopher Southan commented:

IMCO it should have been incumbent on the Bentham Editor-in-Chief, the reviewing Editor and the 3 referees, to have spotted the severe grammatical problems and offered appropriate editorial support. This would have spared these non-native English authors the global embarrassment of publishing such a glaringly broken abstract. However, on checking, it looks like I could be naive in expecting this (https://en.wikipedia.org/wiki/Bentham_Science_Publishers).

On 2017 Apr 21, Manuel Menéndez González commented:

Yes, right. Though that would be an application to adjust pressures. There are many other potential applications where modifying the composition of CSF may represent a treatment of the condition.

On 2017 Apr 18, Darko Lavrencic commented:

I believe that implantable systems for continuous liquorpheresis and CSF replacement  could be successfully used also for intracranial hypotension-hypovolemia syndrome as it could be caused by decreased CSF formation. See: http://www.med-lavrencic.si/research/correspondence/

On 2017 Apr 19, Seán Turner commented:

The authors describe eight (8) new species, not nine (9) as indicated in the title. In the manuscript, the accessions numbers for the 16S rRNA genes of the type strains of Mailhella massiliensis (strain Marseille-P3199) and Mordavella massiliensis (strain Marseille-P3246) are switched; the correct assignments are LT615363: Mailhella massiliensis Marseille-P3199, and LT598584: Mordavella massiliensis Marseille-P3246.

On 2017 Sep 11, Anders von Heijne commented:

In addition to the complications to treatment with fingolimod that the authors report, there are a number of reported cases with PRES, with obviuous radiological implications. In the EudraVigilance database there are currently (september 2017) 21 reported cases of fingolimod-related PRES.

On 2017 Apr 24, Lydia Maniatis commented:

This article’s casual approach to theory is evident in the first few sentences. After noting irrelevantly, that “Since their introduction (Wilkinson, Wilson, & Habak, 1998), RF patterns have become a popular class of stimuli in vision science, commonly used to study various aspects of shape perception,” the authors immediately continue to say that “Theoretically, RF pattern detection (discrimination against a circle) could be realized either by local filters matched to the parts of the pattern, or by a global mechanism that integrates local parts operating on the scale of the entire pattern.” No citation is offered for this vague and breezy assertion, which begs a number of questions.

1. How did we jump from “shape perception” to “RF detection against a circle”? How is the latter related to the former?

2. Is the popularity of a pattern sufficient reason to assume that there exist special mechanisms – special detectors, or filters – tailored to its characteristics? Is there any basis whatsoever for this assertion?

3. Given that we know that the whole does determine the parts perceived, why are we talking about integration of “local” elements? And how do we define local? Doesn’t a piece of a shape also consist of smaller pieces, etc? What is the criterion for designating part and whole in a stimulus pattern (as opposed to the fully-formed percept)?

Apparently, there have been many ‘models’ proposed for special mechanisms for “RF detection against a circle,” addressing the question in these local/local-to-global terms. Could the mechanism involve maximum curvature integration, tangent orientations at inflection points, etc.? These simply take for granted the underlying assumption that there are special “filters” for “RF discrimination against a circle.” The only question is to what details of the figure are these mechanisms attuned.

What if we were dealing with different types of shapes? What if the RF boundary shape were formed by different sized dots, or dashes, or rays of different lengths radiating from a center? Would we be talking about dot filters, or line length filters? Why put RF patterns in general, and RF patterns of this type in particular, on such an explanatory pedestal?

More critically, how is it possible to leverage such patterns to dissect the neural processes underlying perception? When I look at one of these patterns, I don’t have any trouble distinguishing it from a circle. What can this tell me about the underlying process?

A subculture of vision science has opted to uncritically embrace the view that underlying processes can be inferred quite straightforwardly on the basis of certain procedures that mimic the general framework of signal detection. This view is labeled “signal detection theory” or SDT, but “theory” is overstating it. As noted in my earlier comment, Schmidtmann and Kingdom (2017) never explain why they make what, to a naïve observer, must seem very arbitrary methodological choices, nor does their main reference, Wilkerson, Wilson and Habak (1998). So we have to go back further to find some suggestion of a rationale.

The founding fathers of the aforementioned subculture include Swets, Tanner and Birdsall (e.g. 1961). As may be seen from a quote from that article (below), the framing of the problem is artificial; major assumptions are adopted wholesale; “perception” is casually converted to “detection” (in order to fit the analogy of a radar observer attempting to guess which blip is the object of interest).

“In the fundamental detection problem, an observation is made of events occurring in a fixed interval of time and a decision is made; based on this observation, whether the interval contained only the background interference or a signal as well. The interference, which is random, we shall refer to as noise and denote as N; the other alternative we shall term signal plus noise, SN. In the fundamental problem, only these two alternatives exist…We shall, in the following, use the term observation to refer to the sensory datum on which the decision is based. We assume that this observation may be represented as varying continuously along a single dimension…it may be helpful to think of the observation as…the number of impulses arriving at a given point in the cortex within a given time.” Also “We imagine the process of signal detection to be a choice between Gaussian variables….The particular decision that is made depends on whether or not the observation exceeds a criterion value….This description of the detection process is an almost direct translation of the theory of statistical decision.”

In what sense does the above framework relate to visual perception? I think we can easily show that, in concept and application, it is wholly incoherent and irrational.

I submit, first, that when I look around me, I don’t see any noise, I just see things. I’m also not conscious of looking for a signal to compare to noise; I just see whatever comes up. I don’t have a criterion for spotting what I don’t know will come up, and I don’t feel uncertain of - I certainly hardly ever have to guess at – what I’m seeing. The very effortlessness of perception is what made it so difficult to discern the fundamental theoretical problems. This is not, of course, to say that what the visual system does in constructing the visual percept from the retinal stimulation isn’t guesswork; but the actual process is light years more complex and subtle than a clumsy and artificial “signal detection” framework.

Given the psychological certainty of normal perceptual experience, it’s hard to see how to apply this SDT framework. The key seems to be to make conditions of observation so poor as to impede normal perception, making the observer so unsure of what they saw or didn’t see that they must be forced to choose a response, i.e. to guess. One way to degrade viewing conditions is to make the image of interest very low contrast, so that it is barely discernible; another way is to flash it for very brief intervals. Now, in these presentations, the observer presumably sees something; so these manipulations don’t necessarily produce an uncertain perceptual situation (though the brevity of the presentation may make the recollection of that impression mnemonically challenging). Where the uncertainty comes in is in the demand by investigators that observers decide whether the impression is consistent with a quick, degraded glimpse of a particular figure, in this case an RF of a certain type or a circle. I don’t see how one can defend the notion put forth by Swets et al (1961) that this decision, which is more a conscious, cognitive one than a spontaneous perceptual one, is based on a continuously varying criterion. The decision, for example, may be based on a glimpse of one diagnostic feature or another, or on where, by chance, the fovea happens to fall in the 180ms (Schmidtmann and Kingdom, 2017) or 167ms (Wilkerson et al, 1998) interval allowed. But the forced noisiness (due to the poor conditions), the Gaussian presumptions, the continuous variable assumption, and the binary forced choice outputs are needed for the SDT framework to be laid on top of the data.

For rest of comment (here limited by comment size limits), please see PubPeer.

On 2017 Apr 23, Lydia Maniatis commented:

It is oddly difficult to explain why a particular publication has no scientific content, even when, here, this is unequivocally the case. I think it’s important to try and make this quite clear.

Before addressing the serious theoretical problems, I would like to make the easier points that show that, even on its own terms, the project is sloppy and unsuccessful.

According to the authors, whatever it is they are proposing is “physiologically unrealistic” (p. 24). Yet they continue on to say: “Nonetheless, the model presented here will hopefully serve as a basis for developing a more physiological model of LF and RF detection.” There is no rationale offered to underpin this inarticulate hope, which seems even more misplaced given that “there is a modest, systematic mismatch between the [unrealistic] model and the data,” despite the very permissive (three free parameters, the post hoc introduction of a corrective function) model-fitting. That the modeling is strictly post hoc and ad hoc in character is reflected in the following statements: “The CFSF model presented here does not predict the inevitable increase in thresholds at frequencies higher than those explored in the present study. To do so would require CFSF with a somewhat different shape to the one shown in Figure 4…However, because we do not have the requisite data showing an upturn in thresholds at very high frequencies, we have not incorporated this feature into our present model.” (p. 24). We are dealing with atheoretical, condition/data-specific post hoc model-fitting with no heuristic value.

There is also a lack of methodological care in the procedure. As is usual in papers of this type, the number of observers is very small, and they are not all naïve (here, ¾). One is apparently an author (GS). If naivete doesn’t matter, then why mention it, and if it does, why the author participation? Also, while we’re given quite detailed descriptions of many aspects of the stimuli per se – details whose theoretical basis or relevance is unclear - we’re only told that the “monitor’s background was initially set to a mean luminance (grey).” The reference to “grey” is uninformative with respect to actual luminance. The monitor is part of the stimulus. (I don’t understand the reference to “initially.” Maybe I’m missing something.) The following statement also seems strangely casual and vague: “Observers usually completed two experimental blocks for each experimental conditions…” Usually?

As for this: "The cross-sectional luminance profile was defined by a Gaussian with a standard deviation of 0.05 deg" -- it's just a part of the culture, no explanation needed.

And then this - in the context of trying to rationalize differences between the present results and those of previous studies: “In addition to the reported data, we conducted a control experiment to measure detection thresholds for RF and LF patterns with a modulation frequency of 30 for two additional naïve observers. Results show that thresholds are no higher than for a modulation frequency of 20.” Why are we discussing unreported data? Why wasn’t this control experiment reported in the body of the paper?

Experimental stimuli were exposed for 180ms, with a 400ms isi. Why not 500ms, with a 900ms isi? Or something else? 180ms is very short, when we consider the time it takes to initiate a saccade. Was this taken into consideration? Does it matter? In general, on what theoretical basis were conditions selected? Would changing some or all change the results? What would it mean with respect to theory? Is the model so narrowly applicable that it extends only to these specific and apparently arbitrary conditions? If changing conditions would lead to different results, and to different post hoc models, and if the authors can’t predict and assign a theoretical meaning to these different possible outcomes, then it should be clear that the model has no explanatory status, that it is merely an ad hoc mathematical exercise.

The idea that binary forced choices, with their necessary loss of information, are a good idea is mind-boggling, compounded by the arbitrariness of defining “thresholds” based on a 75% correct rate. Why not 99%? (As I'll discuss later, the SDT rationale is wholly inappropriate here). Why wouldn’t vision scientists be interested in what observers are actually seeing, instead of lumping together who knows what impressions experienced under extremely suboptimal conditions? (The reason for this SDT-related, unfortunate indifference to perception by vision scientists will be discussed in a following comment). Generating data in the required form seems more important than understanding what natural phenomena it reflects and explains, if any. Relatedly, I would note that it is indispensible to the evaluation of any visual perception study for the actual stimuli to be presented for interested readers’ inspection. I have asked the authors for access to these stimuli but haven’t yet received a response.

But these are minor problems. The fundamental problem is that the authors have implicitly and explicitly adopted assumptions of visual system function that are never tested and are demonstrably lacking in face validity. (In a nutshell we are talking about the major fallacy of treating perception as a signal detection problem and neurons as "detectors.") In other words, even if the assumptions are false, the experiments premised on them are not designed to reveal this. (Yet, not only do existing facts and logical analysis falsify the premises, it would be easy to design similar experiments within the same framework that would falsify or render its arbitrariness evident, as I'll discuss in my second comment). Rather, data generated are simply assumed to reflect the claimed mechanisms, and loosely, with the help of lots of free parameters and ad hoc manipulations, are perpetually interpreted (via model-fitting) in these terms, with tweaks and excuses for every new and slightly different data set that comes along.

On 2017 Jun 13, John Sotos commented:

To stimulate data-sharing, Bierer et al propose a new type of authorship, "data author," to credit persons who collect data but do not analyze it as part of a scientific study. Their proposal, however, requires a non-trivial modification to the structure of the Pubmed database, revision of authorship criteria across thousands of journals, and assigns a specialness to data authorship that could equally be claimed for "statistical authorship," "drafting authorship," "study-conceiving authorship," "benchwork authorship," etc.

Reviving decades-old proposals for fractional authorship (1) could better achieve the same laudable aims, especially if open-source "blockchain" software technology (2)(3)(4) were used to conveniently, publicly, quantitatively, and securely track authorship credit in perpetuity.

Authorship would thereby have some features of alternate currency (e.g. BitCoin): senior authors could use future authorship credits to "purchase" data from owners according to the data's value. They could also assign roles from a controlled vocabulary (data author, statistical author, etc.) to some or all authors. Over time, norms for pricing and authorship roles would coalesce in the scientific community.

Overall, a blockchain fractional-authorship system would be more flexible and extensible than a special case made for data authors.

(1) Shaw BT. The Use of Quality and Quantity of Publication as Criteria for Evaluating Scientists. Washington, DC: Agriculture Research Service, USDA Miscellaneous Publication No. 1041, 1967. Available at: http://bit.ly/2pVTImI

(2) Nakamoto S. Bitcoin: A Peer-to-Peer Electronic Cash System. October 31, 2008. https://bitcoin.org/bitcoin.pdf

(3) Tapscott D, Tapscott A. Blockchain revolution : how the technology behind bitcoin is changing money, business, and the world. New York: Portfolio / Penguin, 2016

(4) Sotos JG, Houlding D. Blockchains for data sharing in clinical research: trust in a trustless world. (Blockchain Application Note #1.) March 2017. https://simplecore.intel.com/itpeernetwork/wp-content/uploads/sites/38/2017/05/Intel_Blockchain_Application_Note1.pdf

On 2017 Aug 17, NephJC - Nephrology Journal Club commented:

This randomised controlled trial of the C5a Receptor Inhibitor Avacopan in ANCA-Associated Vasculitis., was discussed on May 8th and 9th 2017 on #NephJC, the open online nephrology journal club. Introductory comments written by Tom Oates are available at the NephJC website here

There was significant interest in this promising trial, with 141 participants in the discussion and nearly 700 tweets.

The highlights of the tweetchat were:

• There is a lot of concern in the Nephrology community about the long-term side-effects of steroid use in ANCA vasculitis and that an alternative agent that would allow for lower glucocorticoid exposure would be very welcome.

• Overall, it was thought to be a well-designed and well-conducted trial.

• The chosen primary endpoint, a decrease in Birmingham Vasculitis Activity Score of 50% or more, was hotly debated. Although very frequently used in vasculitis research, using observed changes from baseline as a trial endpoint in a parallel group study may render it a less valid tool.

• The group also questioned whether vaccination would be required with Avacopan however decided that it wouldn’t because it's a receptor blocker unlike Eculizumab which is a complement cleavage inhibitor.

• The treatment response to Avacopan without steroids was excellent and it appears to be a safe drug. We look forward to seeing results of the Phase III studies and some long-term data regarding relapse rates in the absence of steroids.

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 Apr 28, Hilda Bastian commented:

This is an interesting methodological approach to a thorny issue. But the abstract and coverage (such as in Nature glosses over the fact that the results measure the study method's biases more than they measure scientists on Twitter. I think the method is inferring people who are a subset of people working in limited science-based professions.

The list of professions sought is severely biased. It includes 161 professional categories and their plural forms, in English only. It was based on a U.S. list of occupations (SOC) and an ad hoc Wikipedia list. A brief assessment of the 161 titles in comparison with an authoritative international list shows a strong skew towards social scientists and practitioners of some science-based occupations, and away from meical science, engineering, and more (United Nations Educational, Scientific and Cultural Organization (UNESCO)'s nomenclature for fields of science and technology, SKOS).

Of the 161 titles, 17% are varieties of psychologist, for example, but psychiatry isn't there. Genealogists and linguists are there, but geometers, biometricians, and surgeons are not. The U.S. English language bias is a major problem for a global assessment of a platform where people communicating with the general public.

Influence is measured in 3 ways, but I couldn't find a detailed explanation of the calculations or a reference to one, in the paper. It would be great if the authors could point to that here. More detail on the "Who is who" service used in terms of how up-to-date it is would be useful as well.

I have written more about this paper at PLOS Blogs, and point to key numbers that aren't reported, for who was excluded at different stages. The paper says that data sharing is limited by Twitter's terms of service, but it doesn't specify what that covers. Providing a full list of proportions in the 161 titles, and descriptions of more than 15 of the communities they found (none of which appear to be medical science circles), seem unlikely to be affected by that restriction. More data would be helpful to anyone trying to make sense of these results, or extend the work in ways that minimize the biases in this first study.

There is no research cited that establishes the representativeness of data from a method that can only classify less than 2% of people who are on multiple lists. The original application of the method (Sharma, 2011) was aimed at a very different purpose, so representativeness was not such a big issue there. There was no reference in this article to data on list-creating behavior. There could be a reason historians came out on top in this group: list-curating is probably not a randomly-distributed proclivity.

It might be possible with this method to better identify Twitter users who work in STEM fields. Aiming for "scientists", though, remains, it seems to me, unfeasible at scale. Methods described by the authors as product-centric (e.g. who is sharing links to scientific articles and/or discussing them, or discussing blogs where those articles are cited), and key nodes such as science journals and organizations seem essential.

I would also be interested to know the authors' rationale for trying to exclude pseudonyms - as well as the data on how many were excluded. I can see why methods gathering citations for Twitter users exclude pseudonyms, but am not sure why else they should be excluded. A key reason for undertaking this kind of analysis is to understand to what extent Twitter expands the impact of scientific knowledge and research. That inherently means looking to wider groups, and the audiences for their conversations. Thank you to the authors, though, for a very interesting contribution to this complex issue.

On 2017 Aug 06, John Greenwood commented:

(cross-posted from Pub Peer, comment numbers refer to that discussion but content is the same)

To address your comments in reverse order -

Spatial vision and spatial maps (Comment 19):

We use the term “spatial vision” in the sense defined by Russell & Karen De Valois: “We consider spatial vision to encompass both the perception of the distribution of light across space and the perception of the location of visual objects within three-dimensional space. We thus include sections on depth perception, pattern vision, and more traditional topics such as acuity." De Valois, R. L., & De Valois, K. K. (1980). Spatial Vision. Annual Review of Psychology, 31(1), 309-341. doi:doi:10.1146/annurev.ps.31.020180.001521

The idea of a "spatial map” refers to the representation of the visual field in cortical regions. There is extensive evidence that visual areas are organised retinotopically across the cortical surface, making them “maps". See e.g. Wandell, B. A., Dumoulin, S. O., & Brewer, A. A. (2007). Visual field maps in human cortex. Neuron, 56(2), 366-383.

Measurement of lapse rates (Comments 4, 17, 18):

There really is no issue here. In Experiment 1, we fit a psychometric function in the form of a cumulative Gaussian to responses plotted as a function of (e.g.) target-flanker separation (as in Fig. 1B), with three free parameters: midpoint, slope, and lapse rate. The lapse rate is 100-x where x is the asymptote of the curve. It accounts for lapses (keypress errors etc) when performance is otherwise high - i.e. it is independent of the chance level. In this dataset it is never about 5%. However its inclusion does improve estimate of slope (and therefore threshold) which we are interested in. Any individual differences are therefore better estimated by factoring out individual differences in lapse rate. Its removal does not qualitatively affect the pattern of results in any case. You cite Wichmann and Hill (2001) and that is indeed the basis of this three-parameter fit (though ours is custom code that doesn’t apply the bootstrapping procedures etc that they use).

Spatial representations (comment 8):

We were testing the proposal that crowding and saccadic preparation might depend on some degree of shared processes within the visual system. Specific predictions for shared vs distinct spatial representations are made on p E3574 and in more detail on p E3576 of our manuscript. The idea comes from several prior studies arguing for a link between the two, as we cite, e.g.: Nandy, A. S., & Tjan, B. S. (2012). Saccade-confounded image statistics explain visual crowding. Nature Neuroscience, 15(3), 463-469. Harrison, W. J., Mattingley, J. B., & Remington, R. W. (2013). Eye movement targets are released from visual crowding. The Journal of Neuroscience, 33(7), 2927-2933.

Bisection (Comments 7, 13, 15):

Your issue relates to biases in bisection. This is indeed an interesting area, mostly studied for foveal presentation. These biases are however small in relation to the size of thresholds for discrimination, particularly for the thresholds seen in peripheral vision where our measurements were made. An issue with bias for vertical judgements would lead to higher thresholds for vertical vs. horizontal judgements, which we don’t see. The predominant pattern in bisection thresholds (as with the other tasks) is a radial/tangential anisotropy, so vertical thresholds are worse than horizontal on the vertical meridian, but better than horizontal thresholds on the horizontal meridian. The role of biases in that anisotropy is an interesting question, but again these biases tend to be small relative to threshold.

Vernier acuity (Comment 6):

We don’t measure vernier acuity, for exactly the reasons you outline (stated on p E3577).

Data analyses (comment 5):

The measurement of crowding/interference zones follows conventions established by others, as we cite, e.g.: Pelli, D. G., Palomares, M., & Majaj, N. J. (2004). Crowding is unlike ordinary masking: Distinguishing feature integration from detection. Journal of Vision, 4(12), 1136-1169.

Our analyses are certainly not post-hoc exercises in data mining. The logic is outlined at the end of the introduction for both studies (p E3574).

Inclusion of the authors as subjects (Comment 3):

In what way should this affect the results? This can certainly be an issue for studies where knowledge of the various conditions can bias outcomes. Here this is not true. We did of course check that data from the authors did not differ in any meaningful way from other subjects (aside from individual differences), and it did not. Testing (and training) experienced psychophysical observers takes time, and authors tend to be experienced psychophysical observers.

The theoretical framework of our experiments (Comments 1 & 2):

We make an assumption about hierarchical processing within the visual system, as we outline in the introduction. We test predictions that arise from this. We don’t deny that feedback connections exist, but I don’t think their presence would alter the predictions outlined at the end of the introduction. We also make assumptions regarding the potential processing stages/sites underlying the various tasks examined. Of course we can’t be certain about this (and psychophysics is indeed ill-poised to test these assumptions) and that is the reason that no one task is linked to any specific neural locus, e.g. crowding shows neural correlates in visual areas V1-V4, as we state (e.g. p E3574). Considerable parts of the paper are then addressed at considering whether some tasks may be lower- or higher-level than others, and we outline a range of justifications for the arguments made. These are all testable assumptions, and it will be interesting to see how future work then addresses this.

All of these comments are really fixated on aspects of our theoretical background and minor details of the methods. None of this in any way negates our findings. Namely, there are distinct processes within the visual system, e.g. crowding and saccadic precision, that nonetheless show similarities in their pattern of variations across the visual field. We show several results that suggest these two processes to be dissociable (e.g. that the distribution of saccadic errors is identical for trials where crowded targets were correctly vs incorrectly identified). If they’re clearly dissociable tasks, how then to explain the correlation in their pattern of variation? We propose that these properties are inherited from earlier stages in the visual system. Future work can put this to the test.

On 2017 Jul 08, Lydia Maniatis commented:

None

On 2017 Jul 07, Lydia Maniatis commented:

I'm not an expert in statistics, but it seems to me that the authors have conducted multiple and sequential comparisons without applying the appropriate correction. In addition, the number of subjects is small.

Also, the definition of key variables - "crowding zone" and "saccade error zone" - seems arbitrary given that they are supposed to tap into fundamental neural features of the brain. The former is defined as "target-flanker separation at which performance reached 80% correct [i.e. 20% incorrect]...which we take as the dimensions of the crowding zone," the latter by fitting "2D Gaussian functions to the landing errors and defin[ing] an ellipse with major and minor axes that captured 80% of the landing positions (shown with a black dashed line in Fig. 1C). The major and minor axes of this ellipse were taken as the radial and tangential dimensions of the “saccade error zone.”"

What is the relationship between what the authors "take as" the crowding/saccade error zones and a presumptive objective definition? What is the theoretical significance of the 80% cut-off? What would the data look like if we used a 90% cut-off?

Is a "finding" that a hierarchical linear regression "explains" 7.3% of the variance meaningful? The authors run two models, and in one saccades are a "significant predictor" of the data while in the other they are no longer significant, while gap resolution and bisection are. Conclusions seem to be based more on chance than necessity, so to speak.

On 2017 Jul 07, Lydia Maniatis commented:

What would it mean for "crowding and saccade errors" to rely on a common spatial representation of the visual field? The phenomena are clearly not identical - one involves motor planning, for example - and thus their neural substrates will not be identical. To the extent that "spatial map" refers to a neural substrate, then these will not be identical. So I'm not understanding the distinction being made between spatial maps "with inherited topological properties" and "distinct spatial maps."

On 2017 Jul 02, Lydia Maniatis commented:

None

On 2017 Jul 02, Lydia Maniatis commented:

Part 6

With respect to line bisection:

It is mentioned by Arnheim (Art and Visual Perception) that if you ask a person to bisect a vertical line under the best conditions - that is, conditions of free-viewing without time limits - they will tend to place the mark too high:

"An experimental demonstration with regard to size is mentioned by Langfeld: "If one is asked to bisect a perpendicular line without measuring it, one almost invariably places the mark too high. If a line is actually bisected, it is with difficulty that one can convince oneself that the upper half is not longer than the lower half." This means that if one wants the two halves to look alike, one must make the upper half shorter. " (p. 30).

As the authors of this study don't seem to have taken this apparent, systematic bias into account, their "correct" and "incorrect" criterion of line bisection under the adverse conditions they impose may not be appropriate. It is also obvious that the results of the method used did not alert the authors to the possibility of such a bias.

On 2017 Jun 29, Lydia Maniatis commented:

Part 5

With respect to Vernier acuity, and in addition to my earlier objections, I would add that a "low-level" description seems to be at odds with the fact that Vernier acuity, which is also described as hyperacuity, is better than would be expected on the basis of the spacing of the receptors in the retina.

"Yet spatial distinctions can be made on a finer scale still: misalignment of borders can be detected with a precision up to 10 times better than visual acuity. This hyperacuity, transcending by far the size limits set by the retinal 'pixels', depends on sophisticated information processing in the brain....[the] quintessential example and the one for which the word was initially coined,[1] is vernier acuity: alignment of two edges or lines can be judged with a precision five or ten times better than acuity. " (Wikipedia entry on hyperacuity).

When an observer is asked a question about alignment of two line segments, the answer they give is, always, based on the percept, i.e. a high-level, conscious product of visual processing. It is paradoxical to argue that some percepts are high and others low-level, because even if one wanted to argue that some percepts reflect low-level activity, the decision to derive the percept or features thereof from a particular level in one and another level in another case would have to be high-level. The perceived better-than-it-should be performance that occurs in instances of so-called hyperacuity is effectivelyan inference, as are all interpretations of the retinal stimulation, whether a 3D Necker cube or the Mona Lisa. It's not always the case that two lines that are actually aligned will appear aligned. (Even a single continuous line may appear bent - yet line segments are supposed to be the V1 specialty). It all depends on the structure of the whole retinal configuration, and the particular, high-level, inferences to which this whole stimulation give rise in perception.

On 2017 Jun 29, Lydia Maniatis commented:

None

On 2017 Jun 28, Lydia Maniatis commented:

Part 3

I don't understand why it has become normalized for observers in psychophysical experiments to include the authors of a study. Here, authors form one quarter of the participants in the first experiment and nearly one third in the second. Aside from the authors, participants are described as "naive." As this practice is accepted at PNAS, I can only imagine that psychophysical experiments require a mix of subjects who are naive to the purpose and subjects who are highly motivated to achieve a certain result. I only wish the reasons for the practice were made explicit. Because it seems to me that if it's too difficult to find enough naive participants for a study that requires them, then it's too difficult to do the study.

If the inclusion of authors as subjects seems to taint the raw data, there is also a problem with the procedure to which the data are subjected prior to analysis. This essentially untestable, assumption-laden procedure is completely opaque, and mentioned fleetingly in the Methods:

"Psychometric functions were fitted to behavioral data using a cumulative Gaussian with three parameters (midpoint, slope, and lapse rate). "

The key term here is "lapse rate." The lapse rate concept is a controversial theoretical patch-up developed to deal with the coarseness of the methods adopted in psychophysics, specifically the use of forced choices. When subjects are forced to make a choice even when what they perceive doesn't fall into the two, three or four choices preordained by the experimenters, then they are forced to guess. The problem is serious because most psychophysical experiments are conducted under perceptually very poor conditions, such as low contrast and very brief stimulus presentations. This obviously corrupts the data. At some point, practitioners of the method decided they had to take into account this "lapse rate," i.e. the "guess rate." That the major uncertainty incorporated into the forced-choice methodology could not be satisfactorily resolved is illustrated in comments by Prins (2012/JOV), whose abstract I quote in full below:

"In their influential paper, Wichmann and Hill (2001) have shown that the threshold and slope estimates of a psychometric function may be severely biased when it is assumed that the lapse rate equals zero but lapses do, in fact, occur. Based on a large number of simulated experiments, Wichmann and Hill claim that threshold and slope estimates are essentially unbiased when one allows the lapse rate to vary within a rectangular prior during the fitting procedure. Here, I replicate Wichmann and Hill's finding that significant bias in parameter estimates results when one assumes that the lapse rate equals zero but lapses do occur, but fail to replicate their finding that freeing the lapse rate eliminates this bias. Instead, I show that significant and systematic bias remains in both threshold and slope estimates even when one frees the lapse rate according to Wichmann and Hill's suggestion. I explain the mechanisms behind the bias and propose an alternative strategy to incorporate the lapse rate into psychometric function models, which does result in essentially unbiased parameter estimates."

It should be obvious that calculating the rate at which subjects are forced to guess is highly-condition-sensitive and subject-sensitive, and that even if one believes the uncertainty can be removed by a data manipulation, there can be no one-size-fits all method. Which strategy for calculating guessing rate have Greenwood et al (2017) adopted? Why? What was the "lapse rate"? There would seem to be no point in even looking at the data unless their data manipulation and its rationale are made explicit.

On 2017 Jun 27, Lydia Maniatis commented:

Part 2b (due to size limit)

I would note, finally, that unless the authors are also believers in a transparent brain for some, but not other, perceived features resulting from a retinal stimulation event, the idiosyncratic/summative/inherited/low-level effects claims should presumably be detectable in a wide range of normal perceptual experiences, not only in peripheral vision under conditions which are so poor that observers have to guess at a response some unknown proportion of the time, producing very noisy data interpreted in vague terms with a large number of researcher degrees of freedom and a great deal of theoretical special pleading. Why not look for these hypothesized effects where they would be expected to be most clearly expressed?

On 2017 Jun 27, Lydia Maniatis commented:

Part 2 A related and equally untenable theoretical claim casually adopted by Greenwood et al (2017) is one which Teller (1984) has explicitly criticized and Graham (2011) has uncritically embraced and unintentionally satirized. It is the notion that some aspects of perceptual experience are directly related to - and can be used to discern - the behavior of neurons in the "lower levels" of the visual system, usually V1:

"Prior studies have linked variations in both acuity (26) and perceived object size (59) with idiosyncrasies in visual cortical regions as early as V1."

"To consider the origin of the relationship between crowding and saccades, we conducted a second experiment to compare crowding with two "lower-level" measures of spatial localization: gap resolution and bisection thresholds."

"If these similarities were to arise due to an inheritance of a common topology from earlier stages of the visual system, we would expect to see similar patterns of variations in tasks that derive from lower-level processes."

Before addressing the fatal flaws with the theoretical premise, I would like to note that the two references provided in no way rise to the occasion. Both are attempts to link some measures of task performance to area V1 based on fMRI results. fMRI is still a very crude method of studying neural function to begin with. Additionally, the interpretation of the scans is assumption-laden, and we are supposed to take all of the underlying assumptions as given, with no arguments or evidence. For example, from citation 26:

"To describe the topology of a given observer's V1, we fit these fMRI activity maps with a template derived from a conformal mapping method developed by Schwartz (Schwartz 1980, Schwartz 1994). According to Schwartz, two-dimensional visual space can be projected onto the two-dimensional flattened cortex using the formula w=k x log(z + a), where z is a complex number representing a point in visual space, and w represents the corresponding point on the flattened cortex. [n.b. It is well-known that visual experience cannot be explained on a point by point basis]. The parameter a reflects the proportion of V1 devoted to the foveal representation, and the parameter k is an overall scaling factor."

The 1994 Schwartz reference is to a book chapter, and the method being referenced appears to have been proposed in 1980 (pre-fMRI?). I guess we have to take it as given that it is valid.

From ref. 59:

"For pRF spread we used the raw, unsmoothed pRF spread estimates produced by our fine-fitting procedure. However, the quantification of surface area requires a smooth gradient in the eccentricity map without any gaps in the map and with minimal position scatter in pRF positions. therefore, we used the final smoothed prameter maps for this analysis. The results for pRF spread are very consistent when using smoothed parameter maps, but we reasoned that the unsmoothed data make fewer assumptions."

One would ask that the assumptions be made explicit and rationalzed. So, again, references act as window-dressing for unwarranted assertions that the tasks used by the authors directly reflect V1 activity.

The theoretical problem is that finding some correlation between some perceptual task and some empirical observations of the behavior of neurons in some part of the visual system in no way licenses the inference that the perceptual experience tapped by the task is a direction reflection of the activities of those particular neurons. Such correlations are easy to come by but the inference is not tenable in principle. If the presumed response properties of neurons in V1, for example, are supposed to directly cause feature x of a percept, we have to as a. how is this assumption reconciled with the fact that the activities of the same "low-level" neurons underlie all features of the percept and b. how is it that for this feature, all of the other interconnectivities with other neural layers and populations bypassed?

Tolerance for the latter problem was dubbed by Teller (1984) the "nothing mucks it up proviso." As an example of the fallacious nature of such thinking, she refers to the Mach bands and their supposed connection to the responses of ganglion cells as observed via single cell recordings:

"Under the right conditions, the physiological data "look like" the psychophysical data. The analogy is very appealing, but the question is, to what extent, or in what sense, do these results provide an explanation of why we see Mach bands?" (And how, I would add, is this presumed effect supposed to be expressed perceptually in response to all other patterns of retinal stmulation? How does it come about that the responses of ganglion cells are simultaneously shunted directly to perceptual experience, and at the same time participate in the normal course of events underlying visual process as a whole?)

Teller then points out that, in the absence of an explicit treatment of "the constraints that the hypothesis puts on models of the composit map from the peripheral neural level [in this she includes V1] and the bridge locus, and between the bridge locus and phenomenal states," the proposal is nothing more than a "remote homunculus theory," with a homunculus peering down at ganglion cell activity through "a magical Maxwellian telescope." The aganglion cell explanation continues to feature in perception textbooks and university perception course websites.

It is interesting to note that Greenwood et al's first mention of "lower-level" effects (see quote above) is placed between scare quotes, yet nowhere do they qualify the term explicitly.

The ease with which one can discover analogies between presumed neural behavior and psychophysical data was well-described by Graham (2011):

"The simple multiple-analyzers model shown in the top panel of Fig. 1 was and is a very good account, qualitatively and quantitatively, of the results of psychophysical experiments using near-threshold contrasts . And by 1985 there were hundreds of published papers each typically with many such experiments. It was quite clear by that time, however, that area V1 was only one of 10 or more different areas in the cortex devoted to vision. ...The success of this simple multiple-analyzers model seemed almost magical therefore. [Like a magical Maxwellian telescope?] How could a model account for so many experimental results when it represented most areas of the visual cortex and the whole rest of the brain by a simple decision rule? One possible explanation of the magic is this: In response to near-threshold patterns, only a small proportion of the analyzers are being stimulated above their baseline. Perhaps this sparseness of information going upstream limits the kinds of processing that the higher levels can do, and limits them to being described by simple decision rules because such rules may be close to optimal given the sparseness. It is as if the near-threshold experiments made all higher levels of visual processing transparent, therefore allowing the properties of the low-level analyzers to be seen." Rather than challenging the “nothing mucks it up proviso” on logical and empirical grounds, Graham has uncritically and absurdly embraced it. (I would note that the reference to "near-threshold" refers only to a specific feature of the stimulation in question, not the stimulation as a whole, e.g. the computer screen on which stimuli are being flashed, which, of course, is above-threshold and stimulating the same neurons.)

On 2017 Jun 26, Lydia Maniatis commented:

Over thirty years ago, Teller (1984) attempted to inspire a course correction in a field that had become much too reliant on very weak arguments and untested, often implausible assumptions. In other words, she tried to free it from practices appropriate to pseudoscience. Unfortunately, as Greenwood et al (2017) illustrates so beautifully, the field not only ignored her efforts, it became, if anything, even less rigorous.

The crux of Teller's plea is captured by the passage below (emphasis mine). Her reference is to "linking propositions" which she defines as "statements that relate perceptual states to physiological states, and as such are one of the fundamental building blocks of visual science."

"Twenty years ago, Brindley pointed out that in using linking hypotheses, visual scientists often introduce unacknowledged, non-rigorous steps into their arguments. Brindley's remarks correctly sensitized us to the lack of rigor ** with which linking propositions have undoubltedly often been used, but led to few detailed, explicit discussions of linking propositions. it would seem usefule to encourage such discussions, and to encourage visual scientists to make linking propositions explicit **so that linking propositions can be subjected to the requirements of consistency and the risks of falsification appropriate to the evaluation of all scientific [as opposed to pseudoscientific] propositions."

Data itself tells us nothing; it must be interpreted. The interpretation of data requires a clear theoretical framework. One of the requirements of a valid theoretical framework is that its assumptions be a. consistent with each other; b. consistent with known facts; and c. testable, in the sense that it makes new predictions about potentially observable natural phenomena. ("Linking propositions" are effectively just another term for the link between data and theory, applied to a particular field). Theoretical claims, in other words, are not to be made arbitrarily and casually because they are key to the valid interpretation of data.

The major theoretical premise of Greenwood et al (2017_ is arbitrary and inconsistent with the facts aw we know them and as we can infer them logicaly. The authors don't even try to provide supporting citations that are anything more than window-dressing. The premise is contained in the following two exceprted statements:

"Given the hierarchical structure of th eviusal system, with inherited receptive field properties at each stage (35), variations in this topological representation could arise early in the viusal system, with pattenrs specific to each individual that are inherited throughout later stages." (Introduction, p. E3574).

"Given that the receptive fields at each stage in the visual system are likely built via the summation of inputs from the preceding stages (e.g. 58)..." (Discussion, p. E3580).

The statements are false, so it is no surprise that neither of the references provided is anywhere near adequate to support what we are supposed to accept as "given."

The first referenc is to Hubel and Wiesel (1962), an early study recording from the striate cortex of the cat. Its theoretical conclusions are early, speculative, based on a narrow set of stimulus conditions, and apply to a species with rather different visual skills than humans. Even so, the paper does not support Greenwood et al's breezy claim; it includes statements that contradict both of the quoted assertions e.g. (emphasis mine):

"Receptive fields were termed complex when the response to light could not be predicted from the arrangements of excitatory and inhibitory regions. Such regions could generally not be demonstrated; when they could the laws of summation and mutual antagonism did not apply." (p. 151). Even the conclusions that may seem to apply are subject to a conceptual error noted by Teller (1984); the notion that a neuron is specialized to detect the stimulus (of the set selected for testing) to which it fires the fastest. (She likens this error to treating each retinal cone as a detector of wavelength to which it fires the fastest, or at all, when as we know the neural code for color is contingent on relative firing rates of all three cones).

Well before Hubel and Wiesel, it had become abundantly clear that the link between retinal stimulation and perception could not remotely be described in terms of summative processes. (What receptive field properties have been inherited by the neurons whose activity is responsible for the perception of an edge in the absence of a luminance or spectral step? Or an amodal contour? or a double-layer? etc). Other than as a crude reflection of the fact that neurons are all interconnected in some way, the "inherited" story has no substance and no support.

And of course, it is well-known that neural connections in the brain are so extraordinarily dynamic and complex - feedforward, feedback, feed-sideways, diagonally...even the effect of the feedforward component, so to speak, is contingent on the general system state at a given moment of stimulation...that to describe it as "hierarchical" is basically to mislead.

The second supporting citation, to Felleman and van Essen (1991) is also to a paper in which the relevant claims are presented in a speculative fashion.

To be continued (in addition to additional theoretical problems, the method and analysis - mostly post hoc - is also highly problematic).

On 2017 Oct 12, Takashi Shichita commented:

As the comment on PubMed Common, the targeted site of our guide RNA2 was split over Exons 2 and 3. This is our mistake. However, we successfully obtained the Msr1-deficient RAW cell clone through limiting dilution. Our guide RNA1 is thought to function correctly for the disruption of Msr1 gene.

On 2017 Oct 09, Nirajkumar Makadiya commented:

Hi Authors,

Have some questions regarding the methods section of PMID: 28394332. 1) Guide RNA 2 (5′-CTTCCTCACAGCACTAAAAA-3′) for the CRISPR is spanning over exon 2 and 3. Was wondering if that can work? 2) Did you try the other sgRNA sequences to knock out the Msr1 gene?

Thank you!

On 2017 Apr 19, Seán Turner commented:

The accession number for the 16S rRNA gene sequence is incorrectly cited in the manuscript as LN598544.1. The correct number is LT598544.1.

On 2017 Nov 16, David Keller commented:

Thank you, again, for your illuminating and scholarly reply to my comments and questions. Your field of causal inference theory may provide a much-needed bridge spanning the chasm between the land of rigor where mathematicians dwell, and the land of rigor mortis inhabited by clinicians and patients. I will continue to follow your work, and that of your colleagues, with great interest.

On 2017 Nov 16, Ian Shrier commented:

We completely agree on objectives and importance of estimating the per protocol effect. It is absolutely the effect that I am interested in as a patient, and therefore as a physician who wants to communicate important information to the patient.

I do think we have different experiences on how people interpret the words "per protocol analysis". Historically, this term has been used to mean an analysis that does not estimate the per protocol effect except under unusual contexts. More recently, some have used it to refer to a different type of analysis that does estimate the per protocol effect. The field of causal inference is still relatively new and there are other examples of changing terminology. I expect the terminology will stabilize over the next 10 years, which will make it much easier for readers, authors and reviewers.

On 2017 Nov 15, David Keller commented:

Thank you for your thoughtful reply to my comment. In response, I would first remark that, while "it is sometimes difficult to disentangle the jargon", it is always worthwhile to clearly define our terms.

Commonly, an "analysis" is a method of processing experimental data, while an "effect" is a property of experimental data, observed after subjecting it to an "analysis".

As applied to our discussion, the "per protocol effect" would be observed by applying "per protocol analysis" to the experimental data.

My usage of "per protocol results" was meant to refer to the "per protocol effect" observed in a particular trial.

The above commonly-understood definitions may be a reason causal inference terminology "can get quite confusing to others who may not be used to reading this literature", for example, by defining "per protocol effect" differently than as "the effect of per protocol analysis".

Nevertheless, clinicians are interested in how to analyze clinical study data such that the resulting observed effects are most relevant to individual patients, especially those motivated to gain the maximal benefit from an intervention. For such patients, I want to know the average causal effect of the intervention protocol, assuming perfect adherence to protocol, and no intolerable side-effects or unacceptable toxicities. This tells the patient how much he can expect to benefit if he can adhere fully to the treatment protocol.

Of course, the patient must understand that his benefits will be diminished if he fails to adhere fully to treatment, or terminates it for any reason. Still, this "average expected benefit of treatment under ideal conditions" remains a useful goal-post and benchmark of therapy,despite any inherent bias it may harbor, compared with the results of intention-to-treat analysis.