21 April 2020

Some issues in a recent gaming research article: Etindele Sosso et al. (2020)

Research into the possibly problematic aspects of gaming is a hot topic. But most studies in this area have focused on gamers in Europe and North America. So a recent article in Nature Scientific Reports, featuring data from over 10,000 African gamers, would seem to be an important landmark for this field. However, even though I am an outsider to gaming research, it seems to my inexpert eye that this article may have a few wrinkles that need ironing out.

Let’s start with the article reference. It has 16 authors, and the new edition of the APA Publication Manual says that we now have to list up to 20 authors’ names in a reference, so let’s take a deep breath:

Etindele Sosso, F. A., Kuss, D. J., Vandelanotte, C., Jasso-Medrano, J. L., Husain, M. E., Curcio, G., Papadopoulos, D., Aseem, A., Bhati, P., Lopez-Rosales, F., Ramon Becerra, J., D’Aurizio, G., Mansouri, H., Khoury, T., Campbell, M., & Toth, A. J. (2020). Insomnia, sleepiness, anxiety and depression among different types of gamers in African countries. Nature Scientific Reports, 10, 1937. https://doi.org/10.1038/s41598-020-58462-0
(The good news is that it is an open access article, so you can just follow the DOI link and download the PDF file.)

Etindele Sosso et al. (2020) investigated the association between gaming and the four health outcomes mentioned in the title. According to the abstract, the results showed that “problematic and addicted gamers show poorer health outcomes compared with non-problematic gamers”, which sounds very reasonable to me as an outsider to the field. A survey that took about 20 minutes to complete was e-mailed to 53,634 participants, with a 23.64% response rate. After eliminating duplicates and incomplete forms, a total of 10,566 gamers were used in the analyses. The “type of gamer” of each participant was classified as “non-problematic”, “engaged”, “problematic”, or “addicted”, depending on their scores on a measure of gaming addiction, and the relations between this variable, other demographic information, and four health outcomes were examined.

The 16 authors of the Etindele Sosso et al. (2020) article report affiliations at 12 different institutions in 8 different countries. According to the “Author contributions” section, the first three authors “contributed equally to this work” (I presume that this means that they did the majority of it); 12 others (all except Papadopoulos, it seems) “contributed to the writing”; the first three authors plus Papadopoulos “contributed to the analyses”; and five (the first three authors, plus Campbell and Toth) “write [sic] the final form of the manuscript”. So this is a very impressive international collaboration, with the majority of the work apparently being split between Canada, the UK, and Australia, and it ought to represent a substantial advance in our understanding of how gaming affects mental and physical health in Africa.

Given the impressive set of authors and the large scale of this international project (data collection alone took 19 or 20 months, from November 2015 to June 2017), it is somewhat surprising that Etindele Sosso et al.’s (2020) article reports no source of funding. Perhaps everyone involved contributed their time and other resources for free, but there is not even a statement that no external funding was involved. (I am quite surprised that this last element is apparently not mandatory for articles in the Nature family of journals.) The administrative arrangements for the study, involving for example contacting the admissions offices of universities in nine countries and arranging for their e-mail lists to be made available, with appropriate guarantees that each university’s and country’s standards of research ethics would be respected, must have been considerable. The participants completed an online questionnaire, which might well have involved some monetary cost, whether directly paid to a survey hosting company or using up some part of a university’s agreed quota with such a company. Just publishing an Open Access article in Nature Scientific Reports costs, according to the journal’s web site, $1,870 plus applicable taxes.

Ethical approval
One possible explanation for the absence of funding information—although this would still constitute rather sloppy reporting, since as noted in the previous paragraph funding typically doesn’t just pay for data collection—might be if the data had already been collected as part of another study. No explicit statement to this effect is made in the Etindele Sosso et al. (2020) article, but at the start of the Methods section, we find “This is a secondary analysis of data collected during the project MHPE approved by the Faculty of Arts and Science of the University of Montreal (CERAS-2015-16-194-D)”. So I set out to look for any information about the primary analysis of these data.

I searched online to see if “project MHPE” might perhaps be a large data collection initiative from the University of Montreal, but found nothing. However, in the lead author’s Master’s thesis, submitted in March 2018 (full text PDF file available here—note that, apart from the Abstract, the entire document is written in French, but fortunately I am fluent in that language), we find that “MHPE” stands for “Mental Health profile [sic] of Etindele” (p. 5), and that the research in that thesis was covered by a certificate from the ethical board of the university that carries exactly the same reference number. I will therefore tentatively conclude that this is the “project MHPE” referred to in the Etindele Sosso et al. (2020) article.

However, the Master’s thesis describes how data were collected from a sample (prospective size, 12,000–13,000; final size 1,344) of members of the University of Montreal community, collected between November 2015 and December 2016. The two studies—i.e., the one reported in the Master’s thesis and the one reported by Etindele et. al (2020)—each used five measures, of which only two—the Insomnia Severity Index (ISI) and the Hospital Anxiety and Depression Scale (HADS)—were common to both. The questionnaires administered to the participants in the Montreal study included measures of cognitive decline and suicide risk, and it appears from p. 27, line 14 of the Master’s thesis that participants were also interviewed (although no details are provided of the interview procedure). All in all, the ethical issues involved in this study would seem to be rather different to those involved in asking people by e-mail about their gaming habits. Yet it seems that the ethics board gave its approval, on a single certificate, for the collection of two sets of data from two distinct groups of people in two very different studies: (a) a sample of around 12,000 people from the lead author’s local university community, using repeated questionnaires across a four-month period as well as interviews; and (b) a sample of 50,000 people spread across the continent of Africa, using e-mail solicitation and an online questionnaire. This would seem to be somewhat unusual.

Meanwhile, we are still no nearer to finding out who funded the collection of data in Africa and the time taken by the other authors to make their (presumably extensive, in the case of the second and third authors) personal contributions to the project. On p. 3 of his Master’s thesis, the author thanks (translation by me) “The Department of Biological Sciences and the Centre for Research in Neuropsychology and Cognition of the University of Montreal, which provided logistical and financial support to the success of this work”, but it is not clear that “this work” can be extrapolated beyond the collection of data in Montreal to include the African project. Nor do we have any more idea about why Etindele Sosso et al. (2020) described their use of the African data as a "secondary analysis", when it seems, as far as I have been able to establish, that there has been no previously published (primary) analysis of this data set.

Further questions arise when we look at the principal numerical results of Etindele Sosso et al.’s (2020) article. On p. 4, the authors report that “4 multiple linear regression analyses were performed (with normal gaming as reference category) to compare the odds for having these conditions [i.e., insomnia, sleepiness, anxiety, and depression] (which are dependent variables) for different levels of gaming.” I’m not sure why the authors would perform linear, as opposed to logistic, regressions to compare the odds of someone in a given category having a specific condition relative to someone in a reference category, but that’s by no means the biggest problem here.

Etindele Sosso et al.’s (2020) Table 3 lists, for each of the four health outcome variables, the regression coefficients and associated test statistics for each of the predictors in their study. Before we come to these numbers for individual variables, however, it is worth looking at the R-squared numbers for each model, which range from .76 for depression to .89 for insomnia. Although these are actually labelled as “ΔR2”, I assume that they represent the total variance explained by the whole model, rather than a change in R-squared when “type of gamer” is added to the model that contains only the covariates. (That said, however, the sentence “Gaming significantly contributed to 86.9% of the variance in insomnia, 82.7% of the variance in daytime sleepiness and 82.3% of the variance in anxiety [p < 0.001]” in the Abstract does not make anything much clearer.) But whether these numbers represent the variance explained by the whole model or just by the “type of gamer” variable, they constitute remarkable results by any standard. I wonder if anything in the prior sleep literature has ever predicted 89% of the variance explained by a measure of insomnia, apart perhaps from another measure of insomnia.

Now let’s look at the details of Table 3. In principle there are seven variables (“Type of Gamers [sic]” being the main one of interest, plus the demographic covariates Age, Sex, Education, Income, Marital status, and Employment status), but because all of these are categorical, each of the levels except the reference category will have been a separate predictor in the regression, giving a total of 17 predictors. Thus, across the four models, there are 68 lines in total reporting regression coefficients and other associated statistics. The labels of the columns seem to be what one would expect from reports of multiple regression analyses: B (unstandardized regression coefficient), SE (standard error, presumably of B), β (standardized regression coefficient), t (the ratio between B and SE), Sig (the p value associated with t), and the upper and lower bounds of the 95% confidence interval (again, presumably of B).

The problem is that none of the actual numbers in the table seem to obey the relations that one would expect. In fact I cannot find a way in which any of them make any sense at all. Here are the problems that I identified:
-        When I compute the ratio B/SE, and compare it to column t (which should give the same ratio), the two don’t even get close to being equal in any of the 68 lines. Dividing the B/SE ratio by column t gives results that vary from 0.0218 (Model 2, Age, 30–36) to 44.1269 (Model 1, Type of Gamers, Engaged), with the closest to 1.0 being 0.7936 (Model 4, Age, 30–36) and 1.3334 (Model 3, Type of Gamers, Engaged).
-        Perhaps SE refers to the standard error of the standardized regression coefficient (β), even though the column SE appears to the left of the column β? Let’s divide β by SE and see how the t ratio compares. Here, we get results that vary from 0.0022 (Model 2, Age, 30–36) to 11.7973 (Model 1, Type of Gamers, Engaged). The closest we get to 1.0 is with values of 0.7474 (Model 3, Marital Status, Engaged) and 1.0604 (Model 3, Marital Status, Married). So here again, none of the β/SE calculations comes close to matching column t.
-        The p values do not match the corresponding t statistics. In most cases this can be seen by simple inspection. For example, on the first line of Table 3, it should be clear that a t statistic of 9.748 would have a very small p value indeed (in fact, about 1E−22) rather than .523. In many cases, even the conventional statistical significance status (either side of p = .05) of the t value doesn’t match the p value. To get an idea of this, I made the simplifying assumption (which is not actually true for the categories “Age: 36–42”, “Education: Doctorate”, and “Marital status: Married”, but individual inspection of these shows that my assumption doesn’t change much) that all degrees of freedom were at least 100, so that any t value with a magnitude greater than 1.96 would be statistically significant at the .05 level. I then looked to see if t and p were the same side of the significance threshold; they were not in 29 out of 68 cases.
-        The regression coefficients are not always contained within their corresponding confidence intervals. This is the case for 29 out of 68 of the B (unstandardized) values. I don’t think that the confidence intervals are meant to refer to the standardized coefficients (β), but just for completeness, 63 out of 68 of these fall outside the reported 95% CI.
-        Whether the regression coefficient falls inside the 95% CI does not correspond with whether the p value is below .05. For both the unstandardized coefficients (B) and the standardized coefficients (β)—which, again, the CI probably doesn’t correspond to, but it’s quick and cheap to look at the possibility anyway—this test fails in 41 out of 68 cases.

There are some further concerns with Table 3:
-        In the third line (Model 1, “Type of Gamers”, “Problematic”) the value for β is 1.8. Now it is actually possible to have a standardized regression coefficient with a magnitude above 1.0, but its existence usually means that you have big multicollinearity problems, and it’s typically very hard to interpret such a coefficient. It’s the kind of thing that at least one of the four authors who reported in the "Author contributions" section of the article that they "contributed to the analyses" would normally be expected to pick up on and discuss, but no such discussion is to be found.
-        From Table 1, we can see that there were zero participants in the “Age” category 42–48, and zero participants in the “Education” category “Postdoctorate”. Yet, in Table 3, for all four models, these categories have non-zero regression coefficients and other statistics. It is not clear to me how one can obtain a regression coefficient or standard error from a categorical variable that corresponds to zero cases (and, hence, when coded has a mean and standard deviation of 0).
-        There is a surprisingly high number of repetitions of exactly the same value, typically to 3 decimal places, within the same variable, category, and absolute value of the statistic from one model to another. For example, the reported value in the column t for the variable “Age” and category “24–30” is 29.741 in both Models 1 and 3. For the variable “Employment status” and category “Employed”, the upper bound of the 95% confidence interval is the same (2.978) in all four models. This seems quite unlikely to be the result of chance, given the relatively large sample sizes that are involved for most of the categories (cf. Brown & Heathers, 2019), so it is not clear how these duplicates could have arisen.

Table 3 from Etindele et al. (2020), with duplicated values (considering the same variable and category across models) highlighted with a different colour for each set of duplicates. Two pairs are included where the sign changed but the digits remained identical; however, p values that were reported as 0.000 are ignored. To find a duplicate, first identify a cell that is outlined in a particular colour, then look up or down the table for one or more other cells with the same outline colour in the analogous position for one or more other models.

The preprint
It is interesting to compare Etindele Sosso et al.’s (2020) article with a preprint entitled “Insomnia and problematic gaming: A study in 9 low- and middle-income countries” by Faustin Armel Etindele Sosso and Daria J. Kuss (who also appears to be the second author of the published article), which is available here. That preprint reports a longitudinal study, with data collected at multiple time points—presumably four, including baseline, although only “after one months, six months, and 12 months” (p. 8) is mentioned—from a sample of people (initial size 120,460) from nine African countries. This must therefore be an entirely different study from the one reported in the published article, which did not use a longitudinal design and had a prospective sample size of 53,634. Yet, by an astonishing coincidence, the final sample retained for analysis in the preprint consisted of 10,566 participants, which is exactly the same as the published article. The number of men (9,366) and women (1,200) was also identical in the two samples. However, the mean and standard deviation of their ages was different (M=22.33 years, SD=2.0 in the preprint; M=24.0, SD=2.3 in the published article). The number of participants in each of the nine countries (Table 2 of both the preprint and the published article) is also substantially different for each country between the two papers, and with two exceptions—the ISI and the well-known Hospital Anxiety and Depression Scale (HADS)—different measures of symptoms and gaming were used in each case.

Another remarkable coincidence between the preprint and Etindele Sosso et al.’s (2020) published article, given that we are dealing with two distinct samples, occurs in the description of the results obtained from the sample of African gamers on the Insomnia Severity Index. On p. 3 of the published article, in the paragraph describing the respondents’ scores on the ISI, we find: “The internal consistency of the ISI was excellent (Cronbach’s α = 0.92), and each individual item showed adequate discriminative capacity (r = 0.65–0.84). The area under the receiver operator characteristic curve was 0.87 and suggested that a cut-off score of 14 was optimal (82.4% sensitivity, 82.1% specificity, and 82.2% agreement) for detecting clinical insomnia”. These two sentences are identical, in every word and number, to the equivalent sentences on p. 5 of the preprint.

Naturally enough, because the preprint and Etindele Sosso et al.’s (2020) published article describe entirely different studies with different designs, and different sample sizes in each country, there is little in common between the Results sections of the two papers. The results in the preprint are based on repeated-measures analyses and include some interesting full-colour figures (the depiction of correlations in Figure 1, on p. 10, is particularly visually attractive), whereas the results of the published article consist mostly of a fairly straightforward summary, in sentences, of the results from the tables, which describe the outputs of linear regressions.

Figure 1 from the preprint by Etindele Sosso and Kuss (2018, p. 10). This appears to use an innovative technique to illustrate the correlation between two variables.

However, approximately 80% of the sentences in the introduction of the published article, and 50% of the sentences in the Discussion section, appear (with only a few cosmetic changes) in the preprint. This is interesting, not only because it would be quite unusual for a preprint of one study to be repurposed to describe en entirely different one, but also because it suggests that the addition of 14 authors between the publication of the preprint and the Etindele Sosso et al. (2020) article resulted in the addition of only about 1,000 words to these two parts of the manuscript.
The Introduction section of the Etindele and Kuss (2018) preprint (left) and the Etindele et al. (2020) published article (right). Sentences highlighted in yellow are common to both papers.

The Discussion section of the Etindele and Kuss (2018) preprint (left) and the Etindele et al. (2020) article (right). Sentences highlighted in yellow are common to both papers.

Another (apparently unrelated) preprint contains the same insomnia results
It is also perhaps worth noting that the summary of the participants’ results on the ISI measure—which, as we saw above, was identical in every word and number between the preprint and Etindele Sosso et al. (2020)’s published article—also appears, again identical in every word and number, on pp. 5–6 of a 2019 preprint by the lead author, entitled “Insomnia, excessive daytime sleepiness, anxiety, depression and socioeconomic status among customer service employees in Canada”, which is available here [PDF]. This second preprint describes a study of yet another different sample, namely 1,200 Canadian customer service workers. If this is not just another remarkable coincidence, it would suggest that the author may have discovered some fundamental invariant property of humans with regard to insomnia. If so, one would hope that both preprints could be peer reviewed most expeditiously, to bring this important discovery to the wider attention of the scientific community.

Other reporting issues from the same laboratory
The lead author of the Etindele Sosso et al. (2020) article has published even more studies with substantial numbers of participants. Here are two such articles, which have 41 and 35 citations, respectively, according to Google Scholar:

Etindele Sosso, F. A., & Rauoafi, S. (2016). Brain disorders: Correlation between cognitive impairment and complex combination. Mental Health in Family Medicine, 12, 215–222. https://doi.org/10.25149/1756-8358.1202010
Etindele Sosso, F. A. (2017a). Neurocognitive game between risk factors, sleep and suicidal behaviour. Sleep Science, 10(1), 41–46. https://doi.org/10.5935/1984-0063.20170007

In the 2016 article, 1,344 respondents were assessed for cognitive deficiencies; 71.7% of the participants were aged 18–24, 76.2% were women, and 62% were undergraduates. (These figures all match those that were reported in the lead author’s Master’s thesis, so we might tentatively assume that this study used the same sample.) In the 2017 article, 1,545 respondents were asked about suicidal tendencies, with 78% being aged 18–24, 64.3% women, and 71% undergraduates. Although these are clearly entirely different samples in every respect, the tables of results of the two studies are remarkably similar. Every variable label is identical across all three tables, which might not be problematic in itself if similar predictors were used for all of the different outcome variables. More concerning, however, is the fact that of the 120 cells in Tables 1 and 2 that contain statistics (mean/SD combinations, p values other than .000, regression coefficients, standard errors, and confidence intervals), 58—that is, almost half—are identical in every digit. Furthermore, the entirety of Table 3—which shows the results of the logistic regressions, ostensibly predicting completely different outcomes in completely different samples—is identical across the two articles (52 out of 52 numbers). One of the odds ratios in Table 3 has the value 1133096220.169 (again, in both articles). There does not appear to be an obvious explanation for how this duplication could have arisen as the result of a natural process.

Left: The tables of results from Etindele Sosso and Raouafi (2016). Right: The tables of results from Etindele Sosso (2017a). Cells highlighted in yellow are identical (same variable name, identical numbers) in both articles.

The mouse studies
Further evidence that this laboratory may have, at the very least, a suboptimal approach to quality control when it comes to the preparation of manuscripts comes from the following pair of articles, in which the lead author of Etindele Sosso et al. (2020) reported the results of some psychophysiological experiments conducted on mice:

Etindele Sosso, F. A. (2017b). Visual dot interaction with short-term memory. Neurodegenerative Disease Management, 7(3), 182–190. https://doi.org/10.2217/nmt-2017-0012
Etindele Sosso, F. A., Hito, M. G., & Bern, S. S. (2017). Basic activity of neurons in the dark during somnolence induced by anesthesia. Journal of Neurology and Neuroscience, 8(4), 203–207. https://doi.org/10.21767/2171-6625.1000203 [1]

In each of these two articles (which have 28 and 24 Google Scholar citations, respectively), the neuronal activity of mice when exposed to visual stimuli under various conditions was examined. Figure 5 of the first article shows the difference between the firing rates of the neurons of a sample of an unknown number of mice (which could be as low as 1; I was unable to determine the sample size with any great level of certainty by reading the text) in response to visual stimuli that were shown in different orientations. In contrast, Figure 3 of the second article represents the firing rates of two different types of brain cell (interneurons and pyramidal cells) before and after a stimulus was applied. That is, these two figures represent completely different variables in completely different experimental conditions. And yet, give or take the use of dots of different shapes and colours, they appear to be exactly identical. Again, it is not clear how this could have happened by chance.

Top: Figure 5 from Etindele Sosso (2017b). Bottom: Figure 3 from Etindele Sosso et al. (2017). The dot positions and axis labels appear to be identical. Thanks are due to Elisabeth Bik for providing a second pair of eyes.

I find it slightly surprising that 16 authors—all of whom, we must assume because of their formal statements to this effect in the “Author contributions” section, made substantial contributions to the Etindele et al. (2020) article in order to comply with the demanding authorship guidelines of Nature Research journals (specified here)—apparently failed to notice that this work contained quite so many inconsistencies. It would also be interesting to know what the reviewers and action editor had to say about the manuscript prior to its publication. The time between submission and acceptance was 85 days (including the end of year holiday period), which does not suggest that a particularly extensive revision process took place. In any case, it seems that some sort of corrective action may be required for this article, in view of the importance of the subject matter for public policy.

Supporting files
I have made the following supporting files available here
-          Etindele-et-al-Table3-numbers.xls: An Excel file containing the numbers from Table 3 of Etindele et al.’s (2020) article, with some calculations that illustrate the deficiencies in the relations between the statistics that I mentioned earlier. The basic numbers were extracted by performing a copy/paste from the article’s PDF file and using text editor macro commands to clean up the structure.
-          (Annotated) Etindele Sosso, Raouafi - 2016 - Brain Disorders - Correlation between Cognitive Impairment and Complex Combination.pdf” and “(Annotated) Etindele Sosso - 2017 - Neurocognitive Game between Risk Factors, Sleep and Suicidal Behaviour.pdf”: Annotated versions of the 2016 and 2017 articles mentioned earlier, with identical results in the tables highlighted.
-          (Annotated) Etindele Sosso, Kuss - 2018 (preprint) - Insomnia and problematic gaming - A study in 9 low- and middle-income countries.pdf” and “(Annotated) Etindele Sosso et al. - 2020 - Insomnia, sleepiness, anxiety and depression among different types of gamers in African countries.pdf” Annotated versions of the 2018 preprint and the published Etindele et al. (2020) article, with overlapping text highlighted.
-          Etindele-2016-vs-2017.png, Etindele-et-al-Table3-duplicates.png, Etindele-mouse-neurons.png, Etindele Sosso-Kuss-Preprint-Figure1.png, Preprint-article-discussion-side-by-side.png, Preprint-article-intro-side-by-side.png: Full-sized versions of the images from this blog post.

Brown, N. J. L., & Heathers, J. A. J. (2019). Rounded Input Variables, Exact Test Statistics (RIVETS): A technique for detecting hand-calculated results in published research. PsyArXiv Preprints. https://doi.org/10.31234/osf.io/ctu9z

[[ Update 2020-04-21 13:14 UTC: Via Twitter, I have learned that I am not the first person to have publicly questioned the Etindele et al. (2020) article. See Platinum Paragon's blog post from 2020-04-17 here. ]]

[[ Update 2020-04-22 13:43 UTC: Elisabeth Bik has identified two more articles by the same lead author that share an image (same chart, different meaning). See this Twitter thread. ]]

[[ Update 2020-04-23 22:48 UTC: See my related blog post here, including discussion of a partial data set that appears to correspond to the Etindele et al. (2020) article. ]]

[[ Update 2020-06-04 11:50 UTC: I blogged about the reaction (or otherwise) of university research integrity departments to my complaint about the authors of the Etindele Sosso et al. article here. ]]

[[ Update 2020-06-04 11:55 UTC: The Etindele Sosso et al. article has been retracted. The retraction notice can be found here. ]]

[1] This article was accepted 12 days after submission, which is presumably entirely unrelated to the fact that the lead author is listed here as the journal’s specialist editor for Neuropsychology and Cognition.


  1. One other point on the tables from the 2020 article: R^2 and the F value should have a 1:1 relationship, since both are ratios of variance explained to error variance. See https://stats.stackexchange.com/questions/56881/whats-the-relationship-between-r2-and-f-test

    The R^2 values reported do not match the model F values reported.
    Model 1: reported F = 251.87, F implied by R^2 of .89 is 3411
    Model 2: reported F = 184.87, F implied by R^2 of .84 is 2214
    Model 3: reported F = 212.96, F implied by R^2 of .83 is 2059
    Model 4: reported F = 214.48, F implied by R^2 of .76 is 1335

    Note also that, across these models, F and R^2 are not consistently associated: Model 2 has a smaller F value but a larger R^2 than Models 3 and 4; Model 4 has a larger F value but a smaller R^2 than Model 3. Since all analyses have the same degrees of freedom, something is wrong here. (Above and beyond the idea that we can predict 83% of variance in anxiety and 76% of variance in depression just by knowing peoples' sex, age, education, income, marital status, employment, and gamer type.)

    1. Thanks! In fact one of my niche hobbies is back-calculating eta-squared (near enough to R-squared, right?) from the F statistic and the DFs, but I didn't look at it in this case as I had an embarrassment of riches to choose from.

  2. "[1] This article was accepted 12 days after submission, which is presumably entirely unrelated to the fact that the lead author is listed here as the journal’s specialist editor for Neuropsychology and Cognition."

    TBF, "iMedPub" is a polyp of the OMICS entity, so publication in this journal is probably equally unhindered for any other paying contributor.

    1. It appears that Dr Sosso has become disillusioned with iMedPub / OMICS and has asked them to remove his name from the journal's list of editors.

  3. You "wonder if anything in the prior sleep literature has ever predicted 89% of the variance explained by a measure of insomnia"...

    Well, the same author is able to find even better correlations among call centre staff (https://www.medrxiv.org/content/10.1101/19003194v1)

    "Results revealed that duration in position was an excellent predictor of insomnia, sleepiness and anxiety (respectively with R2=91,83%, R2=81,23% and R2=87,46%) but a moderate predictor of depression (R2=69,14%)."

    1. The Nobel Prize people really need to hear about this amazing line of research.

  4. Excellent work! I see that the journal has already put up an EOC on the article. I hope that Etindele Sosso's institution has been alerted to these issues for investigation.

  5. In fact, as his former lab collaborator, I can confirm you guys that I help him sharing this online questionnaire and I can confirm you that at least two cohorts of undergraduates students filled his online questionnaire between 2015 and 2017 (a kind of google form or limewire). His questionnaire really includes variables related to sleep, mood disorders, ethnicity, type of occupation (call center was in) and addiction (it was named « dépendance » in the survey). So no doubt about existence of data for all these papers. But He used to delegate (or pay) analysis to someone else and pretty sure he is not able himself to distinguish duplicate data.I have no idea about his Sci Rep issue, but the rest is true. We alerted him about predatory journals at this period and you can noticed that all these odds publications were made in 2017....I believe other things is going on but there is no misconduct from him, as far i remember.

  6. Well done, Nick

  7. It may be worth noting that the "Mental Health in Family Medicine" that served as an outlet for Sosso et al (2016) is not the same as the "Mental Health in Family Medicine" earlier published by Radcliffe, as the organ of the World Organization of Family Doctors. That fine journal (call it MHFM 1.0) stopped publishing and dropped out of Pubmed indexing in 2013. What we have here (call it MHFM 2.0) began in 2015, charges a £1600 publication fee, and is a product of the predatory publishers 'Open Access Text', OMICS wannabees.

    MHFM 2.0 does include the archives of the old MHFM 1.0, but I am not convinced that it came by them honestly.

  8. FAES is at it again: https://www.sciencedirect.com/science/article/abs/pii/S2352721821001121#!
    The two co-authors appear to be real this time.

  9. https://cdn.publisher.gn1.link/sleepscience.org.br/pdf/v13n1a09.pdf

    Some more of his obviously made up data.

    P values in Table 1 are made up and the data in the scatterplots is clearly not from those questionnaires which have ordinal scores (not continuous).

    Fairly sure Dr Bik would have a field day with the repetitive patterns across Figures 2 and 3. In figure 3 the width of the distribution for pSES keeps changing - so in some scatterplots the max score for that variable is about 5 and sometimes 8. pSES is also an ordinal scale with ten steps so can't be distributed in the continuous way it is plotted.

    That ethical approval number you noticed is there again CERAS-2015-16-194-D.

    The strength of the correlations is incredibly tight. Apparently insomnia is 91% explained by how long you have worked in one place (duration in position)

    Duration in position ranged from 1 to 24 months in the methods text but by three pages later in the scatterplots it ranges from either about 2 (Panels A & B) or about 4 (Panels C & D) in the same figure (2). The top of the range doesn't hit 24 months either and goes down to around 22 months in some panels.