307 Matching Annotations
  1. Last 7 days
  2. Jul 2020
    1. Authors should annotate code before the review occurs because annotations guide the reviewer through the changes

      Guide the reviewer during the review process

    2. It´s also useful to watch internal process metrics, including:

      Inspection rate Defect rate Defect density

    3. Before implementing a process, your team should decide how you will measure the effectiveness of peer review and name a few tangible goals.

      Set few tangible goals. Fix more bugs is not a good example.

    4. Code reviews in reasonable quantity, at a slower pace for a limited amount of time results in the most effective code review.

      Only less than 500 LOC per hour

    5. The brain can only effectively process so much information at a time; beyond 400 LOC, the ability to find defects diminishes.

      <400 LOC

  3. Jun 2020
  4. May 2020
  5. Apr 2020
    1. students responded to messages more actively and engaged in more in-depth discussions when discussions were moderated by a peer.

      This could be a good argument to push Hypothes.is to introduce some sort of moderation, in combination with the finding that annotation threads would be rare, and not very deep (Wolfe & Neuwirth, 2001)

    1. There are good preprints and bad preprints, just like there are with journal articles. Overall, do not be afraid to be scooped or plagiarized! Preprints also actually protect against scooping [21,22]. Preprints establish the priority of discovery as a formally published item. Therefore, a preprint acts as proof of provenance for research ideas, data, code, models, and results—all outputs and discoveries.
      • Salah satu alasan untuk tidak mengunggah preprint adalah takut idenya dicuri,

      • Ini adalah faktor budaya yang lain. Ketakutan yang tidak beralasan. Justru dengan mengunggah preprint, peneliti dapat mengklaim ide lebih awal.

      • Preprint ada yang bagus dan ada yang buruk, peninjauan akan ada di tangan pembaca. Ini adalah hambatan budaya berikutnya, ketika mayoritas pembaca ingin melimpahkan tanggungjawab untuk memverifikasi, memeriksa, dan menjamin kualitas suatu makalah kepada para peninjau.

      • Pengalihan tanggungjawab ini sulit dilakukan ketika dokumen PR sendiri tertutup, dan tidak lepas dari bias.

      • Selain itu, dosen akan menyalahi prinsip yang disebarluaskan kepada para mahasiswa, untuk membaca secara kritis.

    2. One of the reasons is the delay in the peer-review process and the subsequent publication
      • Salah satu kritik terbesar terhadap preprint adalah ketidakadaan peninjauan sejawat (Peer Review/PR).

      • Proses PR ini memang menjadi proses sentral dalam publikasi. Di luar manfaatnya, PR juga dapat merugikan, karena memberikan hambatan waktu.

      • Yang unik ada makalah yang memperlihatkan hasil bahwa banyak makalah versi terpublikasi memiliki isi dan tampilan tidak berbeda dengan versi preprintnya.

    1. Someresearch has shown that preprints tend to be of similar quality to their final published versions in journals
      • Salah satu kritik terbesar terhadap preprint adalah ketidakadaan peninjauan sejawat.

      • Proses PR ini memang menjadi proses sentral dalam publikasi. Di luar manfaatnya, PR juga dapat merugikan, karena memberikan hambatan waktu.

      • Yang unik ada makalah yang memperlihatkan hasil bahwa banyak makalah versi terpublikasi memiliki isi dan tampilan tidak berbeda dengan versi preprintnya.

  6. Mar 2020
    1. Chapman describes the inductive approach as a gathering of facts and taking an inventory of visual qualities in a work. After thoroughly taking in the visual elements, the relationships among these visual elements must be compiled into a summary ofthe impressions that “captures the essence of what we have seen” (p. 80). Chapman also warns against premature judgment and emotional reactions. Only after one has described each part of the work, analyzed the relationship among parts, interpreted these relationships, and summarized the recurrent ideas, can one move onto the judgment by citing the information gathered before the judgment stage.

      Chapman approach

    2. develop constructive approachesto critique (formative, peer-to-peer, self-reflective, summative) that are supportive in intent and that offer alternative points of view.” (AI.18). By Art II: Intermediate, students will “use constructive critical approaches to critique (formative, peer-to-peer, self-reflective, summative).
    3. 1) interpret, reflect on, and evaluate the characteristics, purposes, and merits of personal work and the work of others and 2) identify, analyze, and apply criteria for making visual aesthetic judgments of personal work and the work of others.”

      these are good to include in our learning objectives?

    4. Peer critique in the secondary art classroom:Strategies for best practices

      Peer critique secondary (college?) best practices

    1. I give some display guidelines for them to follow so the presentation looks good and work can be seen easily by all participants. Students who are not finished might use the time to keep working to finish. It is sometimes found that students without work on display are not as interested and they are more apt to offer negative comments. 

      provide display guidelines on how to present the art work.

    2. Successful Art Class Critique

      bookmark

  7. Feb 2020
    1. Transparent Review in Preprints (TRiP) — that enables journals and peer review services to post peer reviews of submitted manuscripts on CSHL’s preprint server bioRxiv.

      Incredible use of annotation technology in peer review over preprints! Watch this space! I'm lucky that I get to use annotation in my work at the Knowledge Futures Group.

  8. Jan 2020
    1. Interested authors can select In Review when they submit their manuscript through Editorial Manager. Participating will enable them to track the progress of their manuscript through peer review with immediate access to review reports, share their work to engage a wider community through open annotation using Hypothesis, follow a transparent editorial checklist, and gain early collaboration and citation opportunities.

      Annotation in peer review, whether on preprints or through a more traditional manuscript submission system, offers the option for reviewers, editors, and authors to give and received feedback in context. And I'm super excited about this new project.

  9. Dec 2019
    1. Furthermore, someone who has just learned something is often better at helping someone else learn it, than is someone who learned it long ago. In addition to older students teaching slightly younger ones, peers can learn from each other in collaborative projects, and they can also serve as peer tutors.

      This definitely supports my idea of peer mentors

    1. Supplementary data

      Of special interest is that a reviewer openly discussed in blog his general thoughts about the state of the art in the field based on what he had been looking at in the paper. This blog came out just after he completed his 1st round review, and before an editorial decision was made.

      http://ivory.idyll.org/blog/thoughts-on-assemblathon-2.html

      This spawned additional blogs that broadened the discussion among the community-- again looking toward the future.<br> See: https://www.homolog.us/blogs/genome/2013/02/23/titus-browns-thoughts-on-the-assemblathon-2-paper/

      And

      https://flxlexblog.wordpress.com/2013/02/26/on-assembly-uncertainty-inspired-by-the-assemblathon2-debate/

      Further the authors, now in the process of revising their manuscript, joined in on twitter, reaching out to the community at large for suggestions on revisions, and additional thoughts. Their paper had been posted in arxiv- allowing for this type of commenting and author/reader interaction See: https://arxiv.org/abs/1301.5406

      The Assemblathon.org site collected and presented all the information on the discussion surrounding this article. https://assemblathon.org/page/2

      A blog by the editors followed all this describing this ultra-open peer review, highlighting how these forms of discussions during the peer review process ended up being a very forward-looking discussion about the state of based on what the reviewers were seeing in this paper, and the directions the community should now focus on. This broader open discussion and its very positive nature could only happen in an open, transparent, review process. See: https://blogs.biomedcentral.com/bmcblog/2013/07/23/ultra-open-peer-review/

  10. Oct 2019
    1. A Million Brains in the Cloud

      Arno Klein and Satrajit S. Gosh published this research idea in 2016 and opened it to review. In fact, you could review their abstract directly in RIO, but for the MOOC activity "open peer review" we want you to read and annotate their proposal using this Hypothes.is layer. You can add annotations by simply highlighting a section that you want to comment on or add a page note and say in a few sentences what you think of their ideas. You can also reply to comments that your peers have already made. Please sign up to Hypothes.is and join the conversation!

  11. Sep 2019
    1. Transparent Review in Preprints will allow journals and peer review services to show peer reviews next to the version of the manuscript that was submitted and reviewed.

      A subtle but important point here is that when the manuscript is a preprint then there are two public-facing documents that are being tied together-- the "published" article and the preprint. The review-as-annotation becomes the cross-member in that document association.

    1. I am writing this review for the Drummond and Sauer comment on Mathur and VanderWeele (2019). To note, I am familiar with the original meta-analyses considered (one of which I wrote), the Mathur and VanderWeele (henceforth MV2019) article, and I’ve read both Drummond and Sauer’s comment on MV2019 and Mathur’s review of Drummond and Sauer’s comment on MV2019 (hopefully that wasn’t confusing). On balance, I think Drummond and Sauer’s (henceforth DSComment) comment under review here is a very important contribution to this debate. I tended to find DSComment to be convincing and was comparatively less convinced by Mathur’s review or, indeed, MV2019. I hope my thoughts below are constructive.

      It’s worth noting that MV2019 suffered from several primary weaknesses. Namely:

      1. On one hand, it didn’t really tell us anything we didn’t already know, namely that near-zero effect sizes are common for meta-analyses in violent video game research.
      2. MV2019, aside from one brief statement as DSComment notes, neglected the well-known methodological issues that tend to spuriously increase effect sizes (unstandardized aggression measures, self-ratings of violent game content, identified QRPs in some studies such as the Singapore dataset, etc.) This resulted in a misuse of meta-analytic procedures.
      3. MV2019 naïvely interprets (as does Mathur’s review of DSComment) near-zero effect sizes as meaningful, despite numerous reasons not to do so given concerns of false positives.
      4. MV2019, for an ostensible compilation of meta-analyses, curiously neglect other meta-analyses, such as those by John Sherry or Furuyama-Kanamori & Doi (2016).

      At this juncture, publication bias, particularly for experimental studies, has been demonstrated pretty clearly (e.g. Hilgard et al., 2017). I have two comments here. MV2019 offered a novel and not well-tested alternative approach (highlighted again by Mathur’s review) for bias, however, I did not find the arguments convincing as this approach appears extrapolative and produces results that simply aren’t true. For instance, the argument that 100% of effect sizes in Anderson 2010 are above 0, is quickly falsified merely by looking at the reported effect sizes in the studies included, at least some of which are below .00. Therefore, this would appear to clearly indicate some error in the procedure of MV2019.

      Further, we don't need statistics to speculate about publication bias in Anderson et al. (2010) as there are actual specific examples of published null studies missed by Anderson et al. (see Ferguson & Kilburn, 2010). Further, the publication of null studies in the years immediately following (e.g. von Salisch et al., 2011) indicate that Anderson's search for unpublished studies was clearly biased (indeed, I had unpublished data at that time but was not asked by Anderson and colleagues for it). So there's no need at all for speculation given we have actual examples of missed studies and a fair number of them.

      It might help to highlight also that traditional publication bias techniques probably are only effective with small sample experimental studies. For large sample correlational/longitudinal studies, effect sizes tend to be a bit more homogeneous, hovering closely to zero. In such studies the accumulation of p-values near .05 is unlikely given the power of small studies. Relatively simple QRPs can make p-values jump rapidly from non-significance to something well below.05. Thus, traditional publication bias procedures may return null results for this pool of studies, despite QRPs, and thus, publication bias having taken place.

      It might also help to note that meta-analyses with weak effects are very fragile to unreported null studies, which probably exist in greater numbers (particularly for large n studies) that would be indicated by publication bias techniques.

      I agree with Mathur’s comment about experiments not always offering the best evidence, given lack of generalizability to real-world aggression (indeed, that’s been a long-standing concern). However, it might help DSComment to note that, by this point, probably the pool of evidence least likely to find effects are longitudinal studies. I’ve got two preregistered longitudinal analyses of existing datasets myself (here I want to make clear that citing my work is by no means necessary for my positive evaluation of any revisions on DSComment), and there are other fine studies (such as Lobel et al., 2017, Breuer et al., 2015, Kuhn et al., 2018; von Salisch et al., 2011, etc.) The authors may also want to note Przybylski and Weinstein (2019) which offer an excellent example of a preregistered correlational study.

      Indeed, in a larger sense, as far as evidence goes, DSComment could highlight recent preregistered evidence from multiple sources (McCarthy et al., 2016; Hilgard et al., 2019, Przybylski & Weinstein, 2019, Ferguson & Wang, 2019, etc.) This would seem to be the most crucial evidence and, aside from one excellent correlational study (Ivory et al.) all of the preregistered results have been null. Even if we think the tiny effect sizes in existing metas provide evidence in support of hypotheses (and we shouldn’t), these preregistered studies suggest we shouldn’t trust even those tiny effects to be “true.”

      The weakest aspect of MV2019 was the decision to interpret near-zero effects as meaningful. Mathur, argues that tiny effects can be important once spread over a population. However, this is merely speculation, and there’s no data to support it. It’s kind of a truthy thing scholars tend to say defensively when confronted by the possibility that effect sizes don’t support their hypotheses. By making this argument, Mathur invites an examination of population data where convincing evidence (Markey, Markey & French, 2015; Cunningham et al., 2016; Beerthuizen, Weijters & van der Laan, 2017) shows that violent game consumption is associated with reduced violence in society. Granted, some may express caution about looking at societal-level data, but here is where scholars can’t have it both ways: One can’t make claims about societal-level effects, and then not want to look at the societal data. Such arguments make unfalsifiable claims and are unscientific in nature.

      The other issue is that this line of argument makes effect sizes irrelevant. If we’re going to interpret effect sizes no matter how near to zero as hypothesis supportive, so long as they are “statistically significant” (which, given the power of meta-analyses, they almost always are), then we needn’t bother reporting effect sizes at all. We’re still basically slaves to NHST, just using effect sizes as a kind of fig leaf for the naked bias of how we interpret weak results.

      Also, that’s just not how effect sizes work. They can’t be sprinkled like pixie dust over a population to make them meaningful.

      As DSComment points out, effect sizes that are this small have high potential for Type 1 error. Funder and Ozer (2019) recent contributed to this discussion in a way I think was less than helpful (to be very clear I respect Funder and Ozer greatly, but disagree with many of their comments on this specific issue). Yet, as they note, interpretation of tiny effects is based on such effects being “reliable”, a condition clearly not in evidence for violent game research given the now extensive literature on the systematic methodological flaws in that literature.

      In her comment Dr. Mathur dismisses the comparison with ESP research, but I disagree with (or dismiss?) this dismissal. The fact that effect sizes in meta-analyses for violent game research are identical to those for “magic” is exactly why we should be wary of interpreting such effect sizes as hypothesis supportive. Saying violent game effects are more plausible is irrelevant (and presumably the ESP people would disagree). However, the authors of DSComment might strengthen their argument by noting that some articles have begun examining nonsense outcomes within datasets. For example, in Ferguson and Wang (2019) we show that the (weak and in that case non-significant) effects for violent game playing are no different in predicting aggression than nonsense variables (indeed, the strongest effect was for the age at which one had moved to a new city). Orben and Przybylski (2019) do something similar and very effective with screen time. Point being, we have an expanding literature to suggest that the interpretation of such weak effects is likely to lead us to numerous false positive errors.

      The authors of DSComment might also note that MV2019 commit a fundamental error of meta-analysis, namely assuming that the “average effect size wins!” When effect sizes are heterogeneous (as Mathur appears to acknowledge unless I misunderstood) the pooled average effect size is not a meaningful estimator of the population effect size. That’s particularly true given GIGO (garbage in, garbage out). Where QRPs have been clearly demonstrated for some studies in this realm (see Przybylski & Weinstein, 2019 for some specific examples of documentation involving the Singapore dataset), the pooled average effect size, however it is calculated, is almost certainly a spuriously high estimate of true effects.

      DSComment could note that other issues such as citation bias are known to be associated with spuriously high effect sizes (Ferguson, 2015), another indication that researcher behaviors are likely pulling effect sizes above the actual population effect size.

      Overall, I don’t think MV2019 were very familiar with this field and, appearing unaware of the serious methodological errors endemic in much of the literature which pull effect sizes spuriously high. In the end, they really didn’t say anything we didn’t already know (the effect sizes across metas tend to be near zero), and their interpretation of these near-zero effect sizes was incorrect.

      With that in mind, I do think DSComment is an important part of this debate and is well worth publishing. I hope my comments here are constructive.

      Signed, Chris Ferguson

    2. [This was a peer review for the journal "Meta-Psychology", and I am posting it via hypothes.is at the journal's suggestion.]

      I thank the authors for their response to our article. For full disclosure, I previously reviewed an earlier version of this manuscript. The present version of the manuscript shows improvement, but does not yet address several of my substantial concerns, each of which I believe should be thoroughly addressed if a revision is invited. My concerns are as follows:

      1.) The publication bias corrections still rely on incorrect statistical reasoning, and using more appropriate methods yields quite different conclusions.

      Regarding publication bias, the first analysis of the number of expected versus observed p-values between 0.01 and 0.05 that is presented on page 3 (i.e., “Thirty nine…should be approximately 4%”) cannot be interpreted as a test of publication bias, as described in my previous review. The p-values would only be uniformly distributed if the null were true for every study in the meta-analysis. If the null does not hold for every study in the meta-analysis, then we would of course expect more than 4% of the p-values to fall in [0.01, 0.05], even in the absence of any publication bias. I appreciate that the authors have attempted to address this by additionally assessing the excess of marginal p-values under two non-null distributions. However, these analyses are still not statistically valid in this context ; they assume that every study in the meta-analysis has exactly the same effect size (i.e., that there is no heterogeneity), which is clearly not the case in the present meta-analyses. Effect heterogeneity can substantially affect the distribution and skewness of p-values in a meta-analysis (see Valen & Yuan, 2007). To clarify the second footnote on page 3, I did not suggest this particular analysis in my previous review, but rather described why the analysis assuming uniformly distributed p-values does not serve as a test of publication bias.

      I would instead suggest conducting publication bias corrections using methods that accommodate heterogeneity and allow for a realistic distribution of effects across studies. We did so in the Supplement of our PPS piece (https://journals.sagepub.com/doi/suppl/10.1177/1745691619850104) using a maximum-likelihood selection model that accommodates normally-distributed, heterogeneous true effects and essentially models a discontinuous “jump” in the probability of publication at the alpha threshold of 0.05. These analyses did somewhat attenuate the meta-analyses’ pooled point estimates, but suggested similar conclusions to those presented in our main text. For example, the Anderson (2010) meta-analysis had a corrected point estimate among all studies of 0.14 [95% CI: 0.11, 0.16]. The discrepancy between our findings and Drummond & Sauer’s arises partly because the latter analysis focuses only on pooled point estimates arising from bias correction, not on the heterogeneous effect distribution, which is the very approach that we described as having led to the apparent “conflict” between the meta-analyses in the first place. Indeed, as we described in the Supplement, publication bias correction for the Anderson meta-analyses still yields an estimated 100%, 76%, and 10% of effect sizes above 0, 0.10, and 0.20 respectively. Again, this is because there is substantial heterogeneity. If a revision is invited, I would (still) want the present authors to carefully consider the issue of heterogeneity and its impact on scientific conclusions.

      2.) Experimental studies do not always yield higher-quality evidence than observational studies.

      Additionally, the authors focus only the subset of experimental studies in Hilgard’s analysis. Although I agree that “experimental studies are the best way to completely eliminate uncontrolled confounds”, it is not at all clear that experimental lab studies provide the overall strongest evidence regarding violent video games and aggression. Typical randomized studies in the video game literature consist, for example, of exposing subjects to violent video games for 30 minutes, then immediately having them complete a lab outcome measure operationalizing aggression as the amount of hot sauce a subject chooses to place on another subject’s food. It is unclear to what extent one-time exposures to video games and lab measures of “aggression” have predictive validity for real-world effects of naturalistic exposure to video games. In contrast, a well-conducted case-control study with appropriate confounding control and assessing violent video game exposure in subjects with demonstrated violent behavior versus those without might in fact provide stronger evidence for societally relevant causal effects (e.g., Rothman et al., 2008).

      3.) Effect sizes are inherently contextual.

      Regarding the interpretation of small effect sizes, we did indeed state several times in our paper that the effect sizes are “almost always quite small”. However, to universally dismiss effect sizes of less than d = 0.10 as less than “the smallest effect size of practical importance” is too hasty. Exposures, such as violent video games, that have very broad outreach can have substantial effects at the population level when aggregated across many individuals (VanderWeele et al., 2019). The authors are correct that small effect sizes are in general less robust to potential methodological biases than larger effect sizes, but to reiterate the actual claim we made in our manuscript: “Our claim is not that our re-analyses resolve these methodological problems but rather that widespread perceptions of conflict among the results of these meta-analyses—even when taken at face value without reconciling their substantial methodological differences—may in part be an artifact of statistical reporting practices in meta-analyses.” Additionally, the comparison to effect sizes for psychic phenomena does not strike as particularly damning for the violent video game literature. The prior plausibility that psychic phenomena exist is extremely low, as the authors themselves describe, and it is surely much lower than the prior plausibility that video games might increase aggressive behavior. Extraordinary claims require extraordinary evidence, so any given effect size for psychic phenomena is much less credible than for video games.

      Signed, Maya B. Mathur Department of Epidemiology Harvard University

      References

      Johnson, Valen, and Ying Yuan. "Comments on ‘An exploratory test for an excess of significant findings’ by JPA loannidis and TA Trikalinos." Clinical Trials 4.3 (2007): 254.

      Rothman, K. J., Greenland, S., & Lash, T. L. (2008). Modern epidemiology (Vol. 3). Philadelphia: Wolters Kluwer Health/Lippincott Williams & Wilkins.

      VanderWeele, T. J., Mathur, M. B., & Chen, Y. (2019). Media portrayals and public health implications for suicide and other behaviors. JAMA Psychiatry.

  12. Aug 2019
  13. Jul 2019
  14. Apr 2019
  15. Feb 2019
    1. Interactions of tomato and Botrytis genetic diversity: Parsing the contributions of host differentiation, domestication and pathogen variation

      This article has a Peer Review Report

  16. Jan 2019
    1. Web annotation, for example, is catching on as a new mode of collaboration, peer review, and other research functions.

      And the combination of community feedback on preprints with traditional and post-publication peer review through collaborative annotation is catching on with a variety of publishers. See InReview by BMC and ResearchSquare. Also COS preprint servers such as SocArXiv and Psyarxiv.