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Impact of blinding on...
Impact of blinding on estimated treatment effects in randomised clinical trials: meta-epidemiological study
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BMJ 2020; 368 doi: https://doi.org/10.1136/bmj.l6802 (Published 21 January 2020) Cite this as: BMJ 2020;368:l6802
Linked Editorial
Blindsided: challenging the dogma of masking in clinical trials
Linked Analysis
Fool's gold? Why blinded trials are not always best
Impact of blinding on estimated treatment effects in randomised clinical trials: meta-epidemiological study - February 05, 2020
Helene Moustgaard, physician14,
Gemma L Clayton, senior research associate in epidemiology5,
Hayley E Jones, senior lecturer in medical statistics and data science5,
Isabelle Boutron, professor of epidemiology6,
Lars Jørgensen, physician4,
David R T Laursen, doctoral student14,
Mette F Olsen, postdoctoral fellow4,
Asger Paludan-Müller, doctoral student4,
Philippe Ravaud, professor of epidemiology6,
Jelena Savović, senior research fellow5 7,
Jonathan A C Sterne, professor of statistics and epidemiology5 7 8,
Julian P T Higgins, professor of evidence synthesis5 7,
Asbjørn Hróbjartsson, professor of evidence-based medicine13
1Centre for Evidence-Based Medicine Odense (CEBMO), Odense University Hospital, Kløvervænget 10, DK-5000 Odense C, Denmark
2Open Patient data Explorative Network (OPEN), Odense University Hospital, Odense, Denmark
3Department of Clinical Research, University of Southern Denmark, Odense, Denmark
4Nordic Cochrane Centre, Copenhagen, Denmark
5Population Health Sciences, Bristol Medical School, University of Bristol, Bristol, UK
6Cochrane France, Hôpital Hôtel-Dieu, Paris, France
7The National Institute for Health Research Collaboration for Leadership in Applied Health Research and Care West (NIHR CLAHRC West) at University Hospitals Bristol NHS Foundation Trust, Bristol, UK
8NIHR Bristol Biomedical Research Centre, University of Bristol, Bristol, UK
Correspondence to: H Moustgaard helene.moustgaard{at}gmail.com (or @HeleneMoustgaa1 on Twitter)
Accepted 19 November 2019
Objectives To study the impact of blinding on estimated treatment effects, and their variation between trials; differentiating between blinding of patients, healthcare providers, and observers; detection bias and performance bias; and types of outcome (the MetaBLIND study).
Design Meta-epidemiological study.
Data source Cochrane Database of Systematic Reviews (2013-14).
Eligibility criteria for selecting studies Meta-analyses with both blinded and non-blinded trials on any topic.
Review methods Blinding status was retrieved from trial publications and authors, and results retrieved automatically from the Cochrane Database of Systematic Reviews. Bayesian hierarchical models estimated the average ratio of odds ratios (ROR), and estimated the increases in heterogeneity between trials, for non-blinded trials (or of unclear status) versus blinded trials. Secondary analyses adjusted for adequacy of concealment of allocation, attrition, and trial size, and explored the association between outcome subjectivity (high, moderate, low) and average bias. An ROR lower than 1 indicated exaggerated effect estimates in trials without blinding.
Results The study included 142 meta-analyses (1153 trials). The ROR for lack of blinding of patients was 0.91 (95% credible interval 0.61 to 1.34) in 18 meta-analyses with patient reported outcomes, and 0.98 (0.69 to 1.39) in 14 meta-analyses with outcomes reported by blinded observers. The ROR for lack of blinding of healthcare providers was 1.01 (0.84 to 1.19) in 29 meta-analyses with healthcare provider decision outcomes (eg, readmissions), and 0.97 (0.64 to 1.45) in 13 meta-analyses with outcomes reported by blinded patients or observers. The ROR for lack of blinding of observers was 1.01 (0.86 to 1.18) in 46 meta-analyses with subjective observer reported outcomes, with no clear impact of degree of subjectivity. Information was insufficient to determine whether lack of blinding was associated with increased heterogeneity between trials. The ROR for trials not reported as double blind versus those that were double blind was 1.02 (0.90 to 1.13) in 74 meta-analyses.
Conclusion No evidence was found for an average difference in estimated treatment effect between trials with and without blinded patients, healthcare providers, or outcome assessors. These results could reflect that blinding is less important than often believed or meta-epidemiological study limitations, such as residual confounding or imprecision. At this stage, replication of this study is suggested and blinding should remain a methodological safeguard in trials.
A randomised clinical trial is the most reliable method for assessing the effect of therapeutic interventions.1 Results of clinical trials underpin evidence based clinical practice and decisions made by regulatory agencies, either directly or as part of a meta-analysis. However, results of randomised clinical trials might be biased2—for example, by systematic differences between the care provided to participants or systematic differences in the behaviour of participants, in the intervention and comparison groups (performance bias); or by systematic differences between these groups in the way in which outcomes are assessed (detection bias). Blinding (sometimes called masking) of patients, healthcare providers, and outcome assessors is intended to prevent such bias.
Blinding is used in some form in about 60% of trials.3 However, blinding of patients and healthcare providers is sometimes not possible owing to the type of interventions being tested (eg, psychotherapy). In other instances, blinding might not be applied owing to logistical challenges. Historically, use of placebo control interventions and blinding procedures was closely linked to early development of the randomised trial. Blinding has been an established methodological principle since around 1950.4
Various meta-epidemiological studies have investigated the effect of blinding on estimated intervention effects.56 Such studies collate large numbers of meta-analyses of randomised trials, compare the results of blinded and non-blinded trials within meta-analyses, and then combine estimated within-meta-analysis differences across meta-analyses.6 Estimates of the average impact of blinding have shown considerable variation between studies.7 These studies mostly dealt with several types of bias simultaneously, and their analyses had conceptual and methodological limitations. Comparison of double blind trials with trials that are not double blinded is problematic, because the double blind concept is ambiguous.89 This ambiguity is especially clear in non-pharmacological trials, and the comparison does not enable separation of performance bias and detection bias. To date, all meta-epidemiological studies of blinding have relied exclusively on information provided by trial publications, where inadequate reporting of blinding is common. Only one study took into account by whom outcomes were reported.10
A more comprehensive analysis of the impact of blinding in randomised trials is important. Designers of trials have to consider whether spending resources on blinding is worthwhile. Users of trial information (eg, consumers, researchers conducting systematic reviews, and guideline developers) must assess the risk of bias due to incomplete blinding.
We conducted a meta-epidemiological study to estimate the separate effects of blinding patients, healthcare providers, and outcome assessors on the results of randomised clinical trials. We also estimated the impact of different types of blinding on between-study heterogeneity.
Identification of meta-analyses for inclusion
We sought meta-analyses that included at least one trial with blinding of patients, healthcare providers, or outcome assessors (that is, observers) and at least one trial without blinding of the same groups. We refer to these as informative meta-analyses. To identify these, we screened all 1042 Cochrane reviews published or updated between 1 February 2013 and 18 February 2014 (Cochrane Database of Systematic Reviews, issue 2, 2013). We used Cochrane risk of bias tool2 assessments to select potentially informative meta-analyses suitable for further data extraction. Specifically, we examined the first listed meta-analysis in the review's table of contents with an observer reported outcome and a difference between trials in the risk of bias score for detection bias (high v low or high v unclear risk); and with a patient reported or healthcare provider decision outcome (outcomes determined by clinical decisions—eg, readmissions or need for surgical intervention) and a difference between trials in the risk of bias score for performance bias.
The screening process identified 395 potentially informative meta-analyses. Of these, 226 provided information on blinding of outcome assessors and 169 on blinding of patients or healthcare providers. For pragmatic reasons, we selected for further study a random subsample of 120 meta-analyses from the former set, but retained all of the latter set, giving a total of 289 potentially informative meta-analyses (full details are in the appendix).
Data retrieval and extraction
Trial publications (and any corresponding protocols/methods publications) were retrieved for each trial in each potentially informative meta-analysis. When publications could not readily be retrieved, we requested a copy from Cochrane review authors. For trials published after 1999 and where the blinding status of trial participants was unclear we contacted authors by email, asking for information on the blinding status of all groups within the trial.
We read the full text of publications in languages known to us (English, Danish, French, German, and Spanish). For publications in other languages (eg, Chinese) we based data extraction on any English language abstract, but did not attempt translation of the full text.
Data on basic trial characteristics and information on blinding status were extracted manually from trial publications. Trial results were extracted automatically from the Cochrane Database of Systematic Reviews through the Archie database interface: number of patients in intervention and control groups, for binary outcomes the number of events, and for measurement scale outcomes the means and standard deviations. We also automated extraction of the name of the Cochrane review group, and review authors' risk of bias assessments for the domains "allocation concealment" and "incomplete outcome data."
Assessment of blinding status
We assessed the blinding status of patients, healthcare providers, and outcome assessors using a modified algorithm derived from that of Akl and colleagues11 (full details are given in the appendix). The algorithm entailed contacting trial authors (for trials published after 1999) when there was insufficient information on blinding in the trial publications. We defined blinding as a lack of awareness by patients, healthcare providers, or outcome assessor of the intervention status of individual patients throughout the trial.
We coded healthcare providers as blinded if all staff groups involved in patient treatment and care were described as "blinded" (eg, doctors and nurses, or all staff), and as non-blinded if all, or a subgroup, were described as "non-blinded" (eg, surgeons). Staff responsible for healthcare provider decision outcomes were thus also covered by the blinding status of healthcare providers.
We differentiated between definitive information on blinding status (definitely yes/definitely no) based on explicit description or contact with trial authors, and assessments based on other information in publications (probably yes/probably no). For instance, for drug trials using a placebo control and described as "double blind" or "triple blind," patients, healthcare providers, and outcome assessors were all classified as blinded (probably yes), unless stated explicitly otherwise. For trials with no mention of "placebo," "double dummy," "double blinding," "triple blinding," "single blinding," or similar, all trial groups were classified as non-blinded (probably no), unless stated explicitly otherwise. Assessment of blinding status was made by two observers independently (AP-M, DRTL, LJ, MFO, HM, or AH), and any differences were resolved by discussion between the two. When we did not receive a reply from authors, or where we did not attempt contact, the blinding status was recorded as unclear.
When making a final determination of whether meta-analyses were informative, and for the purposes of our analyses, we compared trials that had relevant parties recorded as having "definitely no," "probably no," or "unclear" blinding with those that had relevant parties coded as "definitely yes" or "probably yes." After detailed assessment of blinding status, 189 of the 289 meta-analyses were classified as informative.
Classifications and exclusions
Classification of interventions as experimental and control was based on descriptions in the trial publications, except when the review clearly labelled the comparator as "placebo," "control," "standard care," or "treatment as usual," in which case we followed the labelling used by the review authors and classified these interventions as controls. To ensure consistent comparisons of estimated bias across meta-analyses, we excluded those meta-analyses in which intervention classifications were unclear.
Outcome measures were classified as observer reported, patient reported (via interviewer or directly recorded by patients), healthcare provider decision outcomes, or mixed (in instances where the outcome was a mixture of more than one category—eg, both patient and observer reported elements). We excluded meta-analyses of trials that did not all have the same type of outcome (eg, patient reported) unless there was an informative subset of trials with the same type of outcome.
Observer reported outcomes were subdivided into four outcomes: objective—all cause mortality, objective—other than total mortality (eg, automatised non-repeatable laboratory tests), subjective—pure observation (eg, assessment of radiographs), and subjective—interactive (eg, assessment of clinical status). Subjective observer reported outcomes were scored 1-3 according to the degree of subjectivity (that is, the extent to which determination of the outcome depended on the judgment of the observer, with 1 indicating a low degree of subjectivity). The scoring of subjectivity was done by two observers (HM and MFO) independently and masked to any results of trials or meta-analyses, with any differences resolved by discussion. Box 1 shows examples of outcomes and subjectivity scores.
Box 1 Examples of subjectivity scoring of trial outcomes
Subjectivity score 1 (low degree of subjectivity): heart rate, forced expiratory volume in first second (FEV1), cotinine saliva dipstick assay
Subjectivity score 2 (medium degree of subjectivity): superficial surgical site infection, recurrence of varicose veins, tooth prosthesis failure
Subjectivity score 3 (high degree of subjectivity): change in global measure of cognition, Barthel index score (of ability to perform activities of daily living), Hamilton depression scale score
Meta-analyses were classified according to whether the outcome was measured in the trials based on an underlying hypothesis of benefit (eg, degree of pain measured based on the hypothesis that the intervention lowers pain) or of harm (eg, frequency of allergic reactions measured based on the hypothesis that the intervention could cause an increase). Classification of outcomes according to clinical area and type of experimental and comparison interventions was conducted to facilitate comparisons with an earlier meta-epidemiological study.12 We further categorised experimental interventions as alternative/complementary or conventional medicine, to facilitate comparison with a systematic review of trials randomising patients to blinded and unblinded substudies.13
We excluded trials with binary outcomes, in which no or all participants had the outcome event, and trials with continuous outcomes, where the required information for calculating the standardised mean difference was missing. We also excluded trials included in more than one meta-analysis with the same outcome, if the meta-analyses were to be included in the same meta-epidemiological analysis. Such trials were removed at random until the trial occurred only within one meta-analysis. After removal of individual trials, some meta-analyses were no longer informative. The final study database contained 142 meta-analyses with a total of 1153 trials.
All main analyses were prespecified. In our main analyses, which included only meta-analyses with outcomes measured based on a hypothesis of benefit, we differentiated between types of bias (detection bias and performance bias) and category of person blinded (patient, healthcare provider, and outcome assessor). We performed five main analyses, quantifying the average association between estimates of treatment effect and lack of blinding:
(Ia) Blinding of patients in trials with patient reported outcomes (considering a combination of detection bias and performance bias)
(Ib) Blinding of patients in trials with blinded observer reported outcomes (considering performance bias)
(IIa) Blinding of healthcare providers in trials with healthcare provider decision outcomes (considering a combination of detection bias and performance bias)
(IIb) Blinding of healthcare providers in trials with blinded observers or patients assessing the outcome (considering performance bias)
Blinding of outcome assessors (that is, observers) in trials with subjective outcomes (considering detection bias).
We did not primarily focus on trials with objective outcomes, such as all cause mortality, because we did not suspect any marked effect of blinding in such trials. We conducted univariable analyses for each contrast in blinding status using all informative meta-analyses for that characteristic.
Intervention effects for binary outcomes were modelled as log odds ratios and coded such that an odds ratio of less than 1 indicated a beneficial intervention effect. For continuous outcomes, the standardised mean difference and corresponding standard error were used and coded such that a standardised mean difference of less than zero meant a beneficial intervention effect.
We quantified differences in intervention effects, comparing non-blinded trials with blinded trials of each type using ratios of odds ratios: ROR=ORnon-blinded/ORblinded. Bayesian hierarchical models for meta-epidemiological research, developed by Welton and colleagues, were used to estimate the average bias associated with lack of each type of blinding (ROR), the average variability in this bias within a meta-analysis (quantified by ĸ, the standard deviation increase in heterogeneity between trials), and variability in average bias between meta-analyses (quantified by Ф, the standard deviation in mean bias between meta-analyses).14
The model thus enabled us to explore the average degree of bias, and also whether the bias differs (eg, in direction) between meta-analyses (that is, the importance of blinding might depend on the clinical scenario) and between trials (that is, the importance of blinding might depend on factors related to the singular trial, even within similar clinical scenarios).
The analyses were carried out using Markov chain Monte Carlo simulations in WinBUGS version 1.4.3. Vague prior distributions were assumed for all parameters (see appendix for more details). We modelled continuous and binary data simultaneously, assuming a mixture of normal and binomial likelihoods but modelling the underlying bias on the same scale. This method required re-expressing standardised mean differences as odds ratios.15 To reduce risk of spurious findings, we defined a lower threshold of at least 10 meta-analyses for conducting an analysis.
To study the impact of subjectivity scores on the average difference in intervention effect associated with blinding outcome assessors, we extended the model of Welton et al14 to incorporate a three level categorical covariate (low v moderate v high degree of subjectivity) at the meta-analysis level.
In sensitivity analyses, we excluded trials with a classification of blinding status as "unclear" from the analyses. Secondary analyses were stratified by outcome type (eg, objective outcomes and subtypes).
Confounding by other flaws in trial design was assessed in multivariable analyses by re-running each of the five main analyses with adjustment in the model for concealment of the allocation sequence, incomplete outcome data (attrition), trial size, and blinding status of patients. The blinding status of patients was only included in the analysis of outcome assessor blinding (III). We adjusted for each of these characteristics in separate analyses. We did not include combinations of the covariates.
We also conducted post hoc subgroup analyses according to type of outcome data (continuous v binary) and type of comparator (active control v inactive control), calculated the impact of concealment of the allocation sequence on estimated treatment effects, and repeated the main analyses using an alternative label-invariant meta-epidemiological model, proposed recently by Rhodes et al.16 This model removes the constraint that intervention effects are at least as variable among the non-blinded trials as among the blinded trials within each meta-analysis, but was not available when we wrote our protocol.
Finally, to facilitate comparison of our results with previous meta-epidemiological studies we also compared trials described by trial authors as "double blind" or "triple blind" with those not described in this way.
Patients and members of the public were not involved in the research because it was designed to answer a methodological challenge that was not directly dependent on patient priorities, experiences, or participant preferences. The methodological expertise required to plan the study, analyse the results, and write the manuscript was dependent on specialist knowledge and we did not try to identify patients or members of the public with this training to work with.
The final study database contained 142 meta-analyses with a total of 1153 trials. Figure 1 shows the flow of data through the study, from screening to final dataset. We contacted the trial author for 54 (5%) of the 1153 trials in the dataset. In 28 instances the authors replied (response rate 52%), and the fraction of trials with unclear blinding status was thereby reduced from 95/1153 (8%) to 67/1153 (6%). Appendix table 1 shows the proportions of trials classified as definitely yes and probably yes.
Fig 1
Study flow diagram. *Meta-analyses contributing with trials that had outcome measures categorised as "mixed" (that is, it was not possible to classify them as patient reported, healthcare provider decision, or observer reported because they contained elements from more than one of these types) were not counted. Mixed outcome trials did not contribute to the main analyses
Table 1 shows characteristics of the 142 meta-analyses and 1153 trials included in the dataset. The median year of trial publication was 2003 (interquartile range 1996-2008), and the median sample size was 768 (293-2025) patients for meta-analyses and 106 (50-270) for trials. Of the 1153 trials included in the analysis dataset, 1112 (96%) had a parallel trial design and 753 (65%) were drug trials. Full details are given in appendix table 1.
Characteristics of meta-analyses and trials included for the overall dataset and main analyses
Various methodological characteristics were strongly associated across trials. For instance, trials in which the outcome assessor was blinded were more likely to have adequate allocation concealment (odds ratio 3.0, 95% confidence interval 2.2 to 4.0) and complete outcome data (2.0, 1.5 to 2.8). Trials reporting that patients were blinded were more likely to report that the outcome assessor was blinded (75.0, 38.6 to 145.8). Full details are shown in appendix tables 2 and 3. Figure 2 presents results for each of the five main analyses (Ia, Ib, IIa, IIb, III). Forest plots of the meta-analyses are shown in appendix figure 1.
Estimated ratios of odds ratios and effects on heterogeneity associated with blinding status of patients, healthcare providers, and outcome assessors. Unadjusted analyses. *Increase in standard deviation between trials: (Ia) 0.22 (95% credible interval 0.02 to 0.60), (Ib) 0.10 (0.01 to 0.30), (IIa) 0.06 (0.01 to 0.30), (IIb) 0.10 (0.01 to 0.59), (III) 0.05 (0.01 to 0.22). †Standard deviation between meta-analyses: (Ia) 0.20 (95% credible interval 0.01 to 0.74), (Ib) 0.11 (0.01 to 0.55), (IIa) 0.06 (0.01 to 0.26), (IIb) 0.13 (0.01 to 0.82), (III) 0.09 (0.01 to 0.31)
For the effect of blinding patients in trials with patient reported outcomes (analysis Ia), 18 informative meta-analyses with a hypothesis of benefit contained 132 trials. Patient blinding was assessed as probably yes or definitely yes in 33 trials (25%). The average ROR was 0.91 (95% credible interval 0.61 to 1.34). The average standard deviation increase in heterogeneity between trials among non-blinded trials was very imprecisely estimated and is presented in figure 2 and appendix table 4, together with implied 95% predictive intervals for the ROR in a single trial, to facilitate interpretation. For the effect of blinding patients in trials with blinded observer reported outcomes (analysis Ib), 14 informative meta-analyses with a hypothesis of benefit contained 95 trials. Patient blinding was assessed as probably yes or definitely yes in 57 (60%) of these. The average ROR was 0.98 (95% credible interval 0.69 to 1.39).
For the effect of blinding healthcare providers in trials with healthcare provider decision outcomes (analysis IIa), 29 informative meta-analyses with a hypothesis of benefit contained 173 trials. Healthcare provider blinding was assessed as probably yes or definitely yes in 93 of these trials (54%). The average ROR was 1.01 (95% credible interval 0.84 to 1.19). For the effect of blinding healthcare providers in trials with blinded observers or patients assessing the outcome (analysis IIb), 13 informative meta-analyses with a hypothesis of benefit contained 91 trials. Healthcare provider blinding was assessed as probably yes or definitely yes in 61 trials (67%). The average ROR was 0.97 (95% credible interval 0.64 to 1.45).
For the effect of blinding outcome assessors (that is, observers) in trials with subjective outcomes (analysis III), 46 informative meta-analyses with a hypothesis of benefit contained 397 trials. Outcome assessor blinding was assessed as probably or definitely yes in 199 of these trials (50%). The average ROR was 1.01 (95% credible interval 0.86 to 1.18). In the additional analysis in which we explored the impact of the level of subjectivity of the outcome, we estimated average RORs of 0.94 (0.71 to 1.21), 1.05 (0.83 to 1.38), and 1.10 (0.75 to 1.63) for outcomes with low, moderate, and high degree of subjectivity, respectively.
For each of the five main analyses, separate adjustment for concealment of the allocation sequence, attrition, and trial size did not materially change the result (table 2). Estimated increases in heterogeneity between trials and estimates of variability between meta-analyses in average bias also did not change substantially, compared with the unadjusted main analyses.
Adjusted analyses. Data are outcome measure (95% credible interval) unless stated otherwise
Analyses comparing trials described as "double blind" (or "triple blind") with those not so described, or with an unclear status, did not show any effect when they included meta-analyses with any type of outcome (ROR 0.99, 95% credible interval 0.86 to 1.09), nor when they included only meta-analyses with subjective observer reported outcomes and a hypothesis of benefit (1.11, 0.86 to 1.44; table 3). Exclusion of trials with an unclear blinding status from the unadjusted main analyses did not change the results substantially (table 3).
Secondary analyses. Data are outcome measure (95% credible interval) unless stated otherwise
Results of secondary analyses looking separately at the effect of blinding patients, healthcare providers, or outcome assessors across different types of outcomes are shown in appendix table 5. For example, an analysis based on observer reported outcomes classified as objective also showed little evidence of an effect of outcome assessor blinding status (ROR 0.94, 95% credible interval 0.61 to 1.26; meta-analyses with a hypothesis of benefit only).
A pre-planned repetition of the main analyses based only on trials scored as definitely yes versus trials scored as definitely no proved unfeasible due to insufficient numbers of meta-analyses (appendix table 5). A post hoc analysis indicated about 10% exaggeration of the odds ratio in trials without adequate concealment of the allocation sequence (table 3). We report the results of other post hoc analyses for type of outcome (continuous v binary) and type of comparator (active control v inactive control) in table 3.
Results for the five main analyses repeated using the alternative, label-invariant, model of Rhodes et al16 are presented in appendix table 6. The estimates of ROR and of heterogeneity between meta-analyses in bias from both models were similar. Results for heterogeneity between trials were not directly comparable to those for the main model, but indicated a possible increase in heterogeneity among blinded trials, although again the parameter estimates were very imprecise.
We found no evidence of a difference, on average, in estimated treatment effects between randomised clinical trials with and without blinding of patients, between trials with and without blinding of healthcare providers, and between trials with and without blinding of outcome assessors. In all instances the credible intervals were wide, including both considerable difference and no difference. The same pattern was found when comparing trials that were double blind with those that were not. Our findings of an increase in heterogeneity between trials are inconclusive, owing to a lack of information.
Strengths and challenges of the study
The main strengths and originality of our study were that blinding was analysed according to the type of person blinded and due consideration given to the type of outcome. Analysis in this way allowed a separation of the two main types of blinding related bias (performance and detection bias) and enabled a comprehensive analysis that was less reliant on the way in which authors used the phrase "double blind." Also, we had a low proportion of trials with unclear blinding status, partly because we attempted to contact the trial authors. We restricted the main analyses to outcomes measured, based on a hypothesis of benefit, and ensured that interventions considered experimental in our analyses were also regarded as experimental in the individual trials.
The specificity of the comparisons limited the number of trials and meta-analyses that could be included in individual analyses, which restricted the precision of estimated differences between trials with and without the various types of blinding. We planned our sample size pragmatically, primarily based on results of comparisons within trials.13, 171819 Formal power calculations were published after we had planned our study.20
Meta-epidemiological studies are observational and so estimated effects of trial characteristics could be confounded. We adjusted for predefined variables such as allocation concealment, attrition, trial size, and blinding status of patients. Concurrent adjustment for a combination of factors was not feasible, and confounding by unknown or unmeasured factors could have affected results.
Confounding by other methodological characteristics can be expected to exaggerate the estimated effect of lack of blinding, rather than cancel it. Nevertheless, attenuation of the estimated effect of blinding by confounding cannot be ruled out. For instance, more pragmatically conducted trials within a meta-analysis (those with the broadest inclusion criteria and with least control of treatment adherence) could be less likely to have used blinding and could have resulted in less beneficial treatment effects than more explanatory trials. The consequence would be to move the estimated ROR towards 1.
Blinding could have less impact in trials comparing an experimental intervention with an active comparator (that is, not compared with placebo, no treatment, or standard care). Type of comparator, however, did not seem to affect the analysis of outcome assessor blinding, and too few informative meta-analyses precluded additional analyses. Possibly, blinding could have less impact in trials that aim to determine an intention-to-treat effect than in trials aiming to determine a per protocol effect. We did not explore whether the impact of blinding differed according to inferential goal or type of analysis.
Blinding could be lost during the course of a trial,21 which would tend to attenuate the apparent differences between blinded and non-blinded trials. Other factors to consider are a possibly larger impact of non-reporting bias on blinded trials, and misclassification (despite our intensive efforts to classify correctly the blinding status of patients, healthcare providers, and outcome assessors). In general, non-differential misclassification would bias our results towards no impact of lack of blinding.
The generalisability of our results could be affected by the sampling strategy inherent in a meta-epidemiological approach. Thus, inclusion of only meta-analyses containing both blinded and non-blinded trials excludes situations where all trials are blinded (as blinding is considered of paramount importance) or, conversely, areas where all trials tend to be non-blinded. Similarly, review authors might be more likely to include both blinded and non-blinded trials in a meta-analysis when there is no clear difference in effect estimates between the two.
Our estimation of average bias (ROR) was robust with regard to choice of statistical model.1416 The same applied to our analyses of heterogeneity in bias between meta-analyses. The model restriction embedded in the additive model by Welton and colleagues,14 used for our main analyses, however, implies that between-trial heterogeneity among non-blinded trials can only increase (or remain unchanged). We reanalysed our data with an alternative model not restricted by this assumption,16 which was not available when we planned our study. The reanalysis indicated a possible decrease in heterogeneity among non-blinded trials, although estimates were imprecise, and results were also consistent with a considerable increase in heterogeneity between trials. We interpret this result cautiously, to imply that there was insufficient information to determine whether lack of blinding was associated with increased heterogeneity between trials. Few direct comparisons have been published between the newly developed label-invariant model16 and the additive model14 used in our study and in most large meta-epidemiological studies.1222 Analyses of the ROBES study database based on the additive model indicated an increase in heterogeneity between trials among trials with inadequate or unclear concealment of allocation, whereas the label-invariant model indicated a decrease.16
Systematic reviews of meta-epidemiological studies723 identified four studies (comparisons within meta-analyses) estimating the impact of blinding patients, three studies estimating the impact of blinding trial personnel, and four studies estimating the impact of blinding outcome assessors. In all instances, blinding had surprisingly little effect.723 Two additional recent studies partly confirmed this pattern: an analysis of physiotherapy trials24 found little evidence of an impact of blinding of patients or of outcome assessors, and a study of oral health trials25 found no evidence of an impact of blinding of outcome assessors, though some evidence of a moderate effect of patient blinding.
By contrast, three systematic reviews of within-trial comparisons for 51 trials with both blinded and non-blinded outcome assessment found that blinding had a clear effect.171819 For example, non-blinded outcome assessors of subjective26 outcomes exaggerated odds ratios by 36%, on average.17 Similarly, a systematic review of 12 trials randomising patients to blinded and non-blinded substudies reported a pronounced bias due to lack of patient blinding in complementary/alternative medicine trials with patient reported outcomes, exaggerating effect sizes by 0.56 standard deviations.13 Such comparisons within trials have no major risk of confounding. The trial design is rare, however, so to what extent the results could be generalised is not clear.
Results of meta-epidemiological studies comparing double blind trials with trials without (or unclear) double blinding have shown noticeable variation.7 A systematic review by Page and colleagues found an overall 8% exaggeration of odds ratios in trials without double blinding (although confidence intervals overlapped no effect),7 and an exaggeration of 23% when outcomes were subjective.712
Mechanisms and implications
Clarification of the circumstances in which blinding is important in trials, and an empirical assessment of direction and degree of bias, have important and direct implications for the design of future trials, for interpretation of trial results, and for instructions on how to assess risk of bias when conducting systematic reviews. Clarification is also pertinent to the current debate on the balance between reliability and relevance of unblinded patient reported outcome measures (PROMS),2728 and the relative importance of blinded explanatory trials versus unblinded pragmatic trials.29
Convincing theoretical reasons lead us to expect both detection and performance bias in non-blinded trials. Experimental psychology backs the notion that expectations and interest tend to shape human evaluations.3031 Comparisons within trials13171819 provide strong evidence that in specific settings lack of blinding in trials causes considerable bias. Exactly what characterises these settings is unclear, however. We suggest that replication of our study would be valuable, as would updates of the systematic reviews of comparisons within trials, and exploration of the conditions under which blinding is more, or less, important.
Meta-epidemiological studies are often used to assess empirically dimensions of bias in randomised trials, but they could themselves be biased. For example, meta-epidemiological studies of allocation concealment have disclosed an unexpected dependence of impact on type of outcome.12 Theoretically, impact of allocation concealment should not depend on the subjectivity of outcomes.732 We suggest careful consideration of the risk of confounding and of bias, such as bias due to misclassification of methodological characteristics or due to erroneous identification of treatments as experimental and control, in meta-epidemiological studies.33
Blinding has been considered an essential methodological precaution in trials for decades. We did not expect to find that our study does not firmly underpin standard methodological practice. Further, our results are coherent with other meta-epidemiological studies that have reported similar results. The implication seems to be that either blinding is less important (on average) than often believed, that the meta-epidemiological approach is less reliable, or that our findings can, to some extent, be explained by lack of precision. At present, we suggest that assessors of the risk of bias in trials included in a systematic review continue to deal with the implications of lack of blinding for risk of bias, as is done in version 2 of the Cochrane risk of bias tool.34
In conclusion, we found no evidence of a difference, on average, in estimated treatment effect between randomised clinical trials with blinded and non-blinded patients, between trials with blinded and non-blinded healthcare providers, and between trials with blinded and non-blinded outcome assessors. The apparent lack of a major average effect of blinding on estimated treatment effects is surprising to us and is at odds with methodological standard practices. We are unclear to what extent our results show that blinding is less important than previously believed, show the limitations of the meta-epidemiological approach (eg, residual confounding), or show a lack of precision in the comparisons made. Until our study has been replicated, and we have a clearer understanding of which types of trials are susceptible to bias associated with lack of blinding, we suggest that blinding remains an important methodological safeguard in trials in which it is feasible.
What is already known on this topic
Blinding is an established methodological procedure in randomised clinical trials
Empirical estimates of the expected degree of bias in trials due to lack of blinding can help interpret trial results (eg, in a systematic review or clinical guideline) and plan future trials
Previous meta-epidemiological studies have reported variable estimates of the effect of blinding, with little discussion of who was blinded and the type of outcome
This large meta-epidemiological study of 142 Cochrane meta-analyses found no evidence that lack of blinding of patients, healthcare providers, or outcome assessors had an impact on effect estimates in randomised clinical trials, on average
This finding does not support the importance of blinding and is inconsistent with some previous studies; but it is consistent with several other smaller meta-epidemiological studies
The results indicate that blinding, on average, could be less important than previously believed, or could reflect limitations in the meta-epidemiological approach, such as confounding and misclassification; replication of the study is recommended and, at present, no change to methodological practice is suggested
We thank former Cochrane editor in chief David Tovey for providing us with access to the Cochrane Database of Systematic Reviews, and the Nordic Cochrane Centre, particularly Rasmus Moustgaard, for enabling automatic data extraction from the database.
Contributors: AH and HM conceived and organised the study, interpreted the results, and drafted the manuscript. HM also extracted data. GLC analysed the data, interpreted results, and drafted the manuscript. HEJ, JS, IB, PR, JPTH, and JACS conceived the study, interpreted the results, and drafted the manuscript. LJ, DRTL, AP-M, and MFO extracted data and drafted the manuscript. HM is guarantor. The corresponding author attests that all listed authors meet authorship criteria and that no others meeting the criteria have been omitted.
Funding: This study received no specific funding. GLC was funded by a PhD studentship from the Medical Research Council (MRC) Hubs for Trials Methodology Research. HEJ was supported by an MRC Career Development Award in Biostatistics (MR/M014533/1). JS and JPTH are supported by the National Institute for Health Research (NIHR) Collaboration for Leadership in Applied Health Research and Care West (CLAHRC West). JACS and JPTH are NIHR senior investigators (NF-SI-0611-10168 and NF-SI-0617-10145, respectively), are supported by NIHR Bristol Biomedical Research Centre at University Hospitals Bristol NHS Foundation Trust and the University of Bristol, and are members of the MRC Integrative Epidemiology Unit at the University of Bristol. The views expressed are those of the author(s) and not necessarily those of the National Health Service, the NIHR, or the UK Department of Health and Social Care.
Competing interests: All authors have completed the ICMJE uniform disclosure form at www.icmje.org/coi_disclosure.pdf (available on request from the corresponding author) and declare: no support from any organisation for the submitted work; no financial relationships with any organisations that might have an interest in the submitted work in the previous three years; no other relationships or activities that could appear to have influenced the submitted work.
Ethical approval: Not required.
Data sharing: Dataset available from the corresponding author after a post-publication period of 1 year allowing time for follow-up projects.
The lead author affirms that this manuscript is an honest, accurate, and transparent account of the study being reported; that no important aspects of the study have been omitted; and that any discrepancies from the study as planned have been explained.
Dissemination to participants and related patient and public communities: We plan to present our findings at national and international scientific meetings. We also plan to use social media outlets to disseminate findings. We will consider the implication of our findings for assessing the risk of bias in results of randomised trials using version 2 of the Cochrane risk of bias assessment tool.
This is an Open Access article distributed in accordance with the Creative Commons Attribution Non Commercial (CC BY-NC 4.0) license, which permits others to distribute, remix, adapt, build upon this work non-commercially, and license their derivative works on different terms, provided the original work is properly cited and the use is non-commercial. See: http://creativecommons.org/licenses/by-nc/4.0/.
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View ORCID ProfileHelene Moustgaard physician, Gemma L Clayton senior research associate in epidemiology, Hayley E Jones senior lecturer in medical statistics and data science, Isabelle Boutron professor of epidemiology, Lars Jørgensen physician, David R T Laursen doctoral student et al
Moustgaard H, Clayton G L, Jones H E, Boutron I, Jørgensen L, Laursen D R T et al.
Impact of blinding on estimated treatment effects in randomised clinical trials: meta-epidemiological study BMJ 2020; 368 :l6802 doi:10.1136/bmj.l6802
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This level of asset protection is obtained immediately upon completion of the Belize trust formation. Unlike other jurisdictions where there is a determined time period that is established before the asset protection statutes for that jurisdiction enter into effect, the protections on assets placed into a Belize trust are immediate. In other jurisdictions the waiting times for asset protection held in a trust can be as long as five years. This makes a Belize trust ideal for situations requiring expediency in asset protection.
The Belize trust can also be used to hold shares in an offshore company. This allows the settlor to avoid having to disclose ownership of such an asset in his or her country of residence. This can be used for privacy reasons or as part of a tax mitigation strategy. Either way, since the assets, once transferred to the offshore Belize trust, are no longer under the ownership of the settlor, it is a sound and legal method to accomplish such goals.
When used for estate planning, the Belize trust is free of any forced provisions regarding heirship. This means that even if within the settlor's place of residence there are laws regarding forced heirship, by virtue of having all the assets in a Belize trust, the settlor is able to distribute his or her wealth the way they deem fit. This is possible because technically the assets no longer belong to the estate of the settlor, therefore they cannot be subject to any forced heirship provisions. The Belize trust in that capacity has a de facto function of a last will and testament for the settlor free of the detracting factors of a traditional will. There is no delay caused by having to wait for probate or other court delays following the death of the settlor or any beneficiary.
In the case of the passing of the settlor, the trustee simply follows that which the settlor had stipulated in the trust deed agreement in the event of death. These provisions can include precise instructions regarding how and when any assets held in the trust are distributed or liquidated. Likewise, they can also include instructions for an asset to continue in operation with the beneficiaries being issued regularly scheduled provisions from the earnings that are continuously being generated from the assets in trust. A practical example of this would be the continuous operation of a company for the benefit of the beneficiaries even after the death of the settlor, whom may have founded the company. The trust continues functioning in an uninterrupted fashion. In the event of the death of a beneficiary, the assets held in trust can be transferred to a new beneficiary without the payment of an inheritance tax.
Operationally and administratively, contingencies are set in place by the formation and administrative agent to ensure that the death of a trustee or protector do not interfere with the functioning of the trust. This is usually handled by naming single or multiple successor trustees and protectors starting at the moment of the Belize trust formation. That way, the continuity of a Belize trust is never affected by the passing of either a trustee or protector.
As far as privacy and compliance is concerned, the Belize offshore trust is neither legally required nor susceptible to being audited. Additionally, the beneficiaries and settlors of a Belize offshore trust are not required to be publicly disclosed. Likewise, the assets held in the trust are also not publicly disclosed. As a matter of fact, the entire document known as the trust deed that contains the names of the beneficiaries, the settlor, the list of assets and that stipulates the instructions for the management and disposition of the assets in the trust by the trustee are never filed publicly. The public registrar for offshore Belize trusts only records the name of the trustee, protector and any successor trustees and protectors selected at the moment of formation. There is no annual tax assessed on these types of trusts by Belize.
The procedure for the offshore Belize trust formation does not require the settlor or the beneficiaries to be present in Belize. The process can be handled entirely by W.I.S. There are, however, certain qualifying items that must be kept in mind. In order to form a Belize offshore trust the settlor and the beneficiaries must not be residents of Belize. Also, any land assets placed in the trust cannot be located in Belize.
W.I.S. will usually offer the service of trust agent for the newly formed entity. The trust agent fulfills the role of trustee. A protector is not a formal requirement for a Belize offshore trust, but if one is desired by the settlor, W.I.S. can also assist in procuring one. The only names that appear in the public registrar are those of the trustee and the protector, never those of the settlor or the beneficiaries.
W.I.S. will also provide advice and assistance in the preparation of the trust deed. This is the major document that transmits the instructions and wishes of the settlor for the way that the trustee is to manage the assets held in the trust. This also names who the beneficiaries are to be and lists the assets that are to be held by the trust. This document is never filed in any public registrar, it is entirely confidential. Only the trustee or trust agent retains a copy and they are bound by confidentiality. Once formed a Belize offshore trust has a maximum duration lasting 120 years.
The versatility and strength of a Belize offshore trust in terms of asset protection, estate planning and tax mitigation position it as one of the best vehicles in one the most stable jurisdictions. The ease of forming a Belize trust especially when using the services of W.I.S. makes it a wise choice for individuals and companies seeking all of the benefits previously described along with a high degree of privacy and confidentiality.


英文摘要 Nowadays, Germany is known for business and technology in the world. Although it was forbid to develop nuclear weapons according to the regulations of the United Nations after World War II and its military power cannot be compared with United States, the government still puts much attention on cultural cooperation in foreign relations with German language, music and tourism assets.
The essential of this thesis is based on the book "soft power" by American scholar Joseph S. Nye. Soft power is contrary to hard power which is mainly used for military power. Through the foreign cultural and educational policy, Cultural diversity can be as a bridge between cultural heritage and the culture of the future.
The studies found that soft power plays an important role in Germany cultural diplomacy and it is the best strategy for world peace and nation brand. Germany begins to have a good prestige after World War II. With great success in economic and cultural promotion, Germany is expected to be an excellent cultural nation in the world.
Cliffs, New Jersey: Prentice Hall, Inc.
Geoffrey Hartman(1997), The Fateful Question of Culture, New York.
Deutschlands, 14th edition, München: Piper.
Society, translation from Max Weber, Wirtschaft und Gesellschaft, 2nd ed.
(1925), Cambridge: Harvard University Press.
Travel, 3rd Edition, Upper Saddle River, N.J. : Pearson Prentice Hall.
perspectives on SME policies and practices, Amsterdam : Elsevier.
Internal Market on the Tourism Sector", Brussels, 1993.
Allgemeine Zeitung, Nr.145, 26. Juni 2010, p.37.
Landscape", Wien : Springer, 2004.
Tourism Conference speech, paper 1-14.
Journal of International Relations, vol.5, no3.
Bundesregierung Nr. 103-1, availible from: http://www.bundespraesident.
Kulturpolitik 2008/2009, Kultur- und Kommunikationsabteilung, 2010.
In Der Welt, Netzwerk Deutsch, 2010.
Goethe-Institut e.V. Hauptstadtbüro Berlin, 2009.
Goethe-Institut e.V. Hauptstadtbüro Berlin, 2010.
München: Goethe-Institut e.V. Zentrale, Februar 2008, P.6.
der Bundesregierung für Kultur und Medien.
Bundersregierung für Kultur und Medien, Berlin.
Creative Industries Initiative of the Federal Government.
GNTB/EITW (European Institute for the Meetings Industry).
and sales for "Destination Germany", German National Tourist Board.
runs from April 24-26, Deutsche Welle, available from: http://www.dw-world.


膽痛(Colic, bilious): Nux V., Coloc., Merc., Puls.
胃脹氣絞痛(Colic, flatulent): Carbo V., Nux V., Sulph.
小孩腹絞痛(Colic, of infants): Cham., Bell., Ipeca.
痔絞痛(Colic, Haemorrhoidal): Nux V., Sulph., Carbo V.
肝絞痛(Colic, hepatic of the liver): Merc.,Nux v., China.
腎絞痛(Colic, nephretic, of the kidney): Canth., Merc.
鉛中毒絞痛(Colic, painter's): Opi., Bell., Plat.
蛔蟲等寄生蟲引起的絞痛(Colic from worms): Merc., Cina., Sulph.
結腸炎(Colitis): 結腸發炎,Bell.,Merc., Bry., Ars., Puls.
預防:那些必須到沼澤地帶、咖啡或茶園、森林或瘧疾地區居住或露營的人,為了強化他們發燒的免疫系統,可以早上起床時吃Sulph.,晚上上床前吃 Nux V.,以使腸子運用正常;早上十時吃一劑 Acon. N.,下午四時吃一劑 Bry.,吃一天,隔天吃 China和 Ars.
急性肝炎需要Acon.,或者Acon.和Bell.替換;發燒時,以Bry.和Merc. 替換;發燒過後,可用Nux.v, Cham., China, Phos., Sulp.
Ars., Canth., Helon., Phos., Tereb.
China, Ars., Phos., Sulp., Calc-c. Ferrum.
有佔有的想法: Opi., Puls., Bell., Ars., Plat., Ign., Lach.
非常成左箕茪雓OPuls. 3和Calc. C. 3, Teucrium, Phos., Thuya, Merc., 和Hepar Sulph.
腫大和嘴巴、喉嚨變黑: Ars., Merc.S., Hep. S.
喉嚨有潰瘍: Bell., Merc. S., Thuya, Hep. S.
懸雍垂下垂: Bell., Merc. S., Nux. V.
喉嚨有粒狀: Bell., Merc. S., Hep. S., Iod., Sulp.
黏液: Bell., Merc. S., Hep. S., Lach.
生壞疽現象: Ars., Merc. S., Hep. S., Lach.
白喉: Merc. Cyan. 和Ars交換,同時Hep. S.,和Iod.


text:
Rolex "Presidents' Watch" Exhibition in Singapore
The showcase celebrates the iconic timepiece, alongside its new Oyster Perpetual Day-Date 40 editions
End: 10 Feb 2016
Location: Rolex Boutique The Hour Glass, and Emperor Watch & Jewellery
Address: Singapore
By Natalie White
Rolex is set to host an exclusive exhibition celebrating the "Presidents' Watch", launched in 1956, alongside a showcase of its new Oyster Perpetual Day-Date 40 editions at 2 of its retail partners in Singapore.
The origin of the nickname for the timepiece originated from the gifting of the 150,000th officially certified Rolex to U.S. General Dwight D. Eisenhower, who was the NATO Commander in Chief of Europe at the time, and later became President of the United States. This Rolex Dayjust with Jubilee band was the first "Rolex President."
Later, Lyndon B. Johnson and Ronald Reagan would also adorn variations of the Datejust and Day-date with the same bracelet design, and therein cemented the reputation of the Rolex watch as the preferred choice for Presidents.
The new generation of this symbol of excellence and prestige was unveiled in 2015, featuring new standards of chronometric performance with the Calibre 3255, as well as modernized aesthetics emblematic of this iconic timepiece.
Visitors are invited to discover the history of the Day-Date through information panels, presented on an impressive structure inspired by the model's iconic President bracelet.
In addition to 3D videos, stories, archive photographs and an exploded view of a movement, several of the new collection's models are on display.
The Day-Date 40 Exhibition can be viewed at Rolex Boutique The Hour Glass at ION Orchard, from 11 to 24 January; and at Emperor Watch & Jewellery at Wisma Atria, from 26 January to 10 February.
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redpajama_set_name: RedPajamaCommonCrawl


In this dip candle carving class, we will learn to carve wonderfully colorful candles into beautiful creations! All ages welcome; under 8 should be supervised by an adult. Cost is only $20, and space is limited, so sign up today!


The man needs no introduction and along with May day, entire Tamilnadu also rejoices for this great man's birthday. Ofcourse we all jointly celebrated Thala's birthday yesterday with a lot of pomp and pleasure.
Here is a look at how our Thala celebrated his birthday. Having turned 43 this year, Thala Ajith was happy about his completion of Veeram that released earlier this year. Wanting to spend some quality with family, Thala spent his birthday his near and dear ones including his best buddies.
Known for his humane nature and knowing the generous contributions he does on his birthday, there were blood donation camps done at various places. Of course the fans also had a fun time cutting cakes for their thala.
What was amazing to find out was that over 2000 fans gathered at his residence at Thiruvanmiyur to celebrate and rejoice. Ofcourse with the social media in boom, fans went crazy in conveying their wishes. Tweets counting up to a few thousands and Facebook statuses adding up to few thousands too went viral, all dedicated to the wonderful man.
This birthday yet again was celebrated in a special manner considering the movie 'Amarkalam', the first movie with wife Shalini, his 25th film in his career was re-released at many places. The one's who love the outdoors chose this option. Ofcourse the television lovers chose to watch him on screen, at home at the comfort of their couch. 'Veeram' blocked for the evening primetime was the one much awaited amongst all. 'Aarambam' too was telecast on TV, which ofcourse was also one of his hit film in the recent past.
We definitely can understand how happy every fan was celebrating one of the wonderful actors' of South India's birthday. Raaga.com takes this occasion to wish the actor many more years of success.


VR's very specific set of hardware requirements is already influencing the components that go into your PC.
Strapping a pair of virtual-reality goggles to one's face used to be the province of bad science fiction. Now, seemingly overnight, VR is here in the real world and dictating the future of the PC.
Why? Because virtual reality—and its cousin, augmented reality—is something of a Holy Grail for the PC industry: a device with potentially mass-market appeal, and one that demands premium components that Silicon Valley has historically struggled to justify. Customers and vendors alike instinctively understand how to use VR. And the price, while high, is within reach of most PC buyers.
Just as importantly, content creators have seemingly embraced it, helping soothe concerns that VR will be just another product in search of a purpose, like 3D TV.
What excites the PC industry most, though, is that while the public thinks of VR as a consumer-electronics device, the technology depends on the PC and its various chips. "We think that the PC will not be just the center of the ecosystem, but on the leading edge of what people do with VR," said Kim Pallister, the director of content planning at Intel.
VR has its roots in gaming, but backers hope it will transcend PC gaming's niche standing to become a more mainstream pastime. Given that gaming hardware sales should top $26 billion this year, that would be quite a feat. The potential of the new, emerging VR market has chip companies slavering—and that's why you're hearing about VR so much.
"When you think about AMD, you think about three things: You think about gamers, you think about VR, and you think about VR experiences," Lisa Su, the chief executive of AMD, said at a GDC press conference.
But gaming and VR experiences differ. PC gamers obsess over higher and higher resolutions, and try to balance that desire with "playable" frame rates, 60fps being the standard threshold. But in VR, frame rates aren't academic: They determine whether you'll enjoy the experience, or lose your lunch.
One of today's high-profile VR headsets, the HTC Vive allows "roomscale," mobile VR, albeit while tethered to a PC.
VR headsets like the Oculus Rift and the HTC Vive are locked at a 2160x1200 resolution, at 90Hz. That makes achieving 90 frames per second an absolute requirement for VR: Input that drops below that will cause the VR images to jutter and stall, creating "simulator sickness." It's enough of an issue that Oculus reportedly handed out a list of "barf-o-meter" ratings for its games at a recent press event. I can attest that even Minecraft, a relatively sedate game, gave me vertigo.
That 90fps minimum will ripple through the industry, executives say. "It's going to absolutely influence chip design," Frank Soqui, the general manager of the enthusiast desktop group at Intel, said in an interview.
The Oculus Rift, now owned by Facebook, was the VR device that first captured the imagination of gamers.
Since GPUs from either AMD or Nvidia can be used to power VR, each company has begun positioning itself as the premier VR hardware partner. Nvidia's VRWorks technology uses multi-resolution shading to avoid rendering pixels that aren't viewable by the user, and warps the image to make it more comfortable to view with a VR headset. AMD has its own technology, known as LiquidVR, which also performs image warping. Both AMD and Nvidia are also encouraging PC makers to consider using multi-GPU rendering, with each GPU's output sent to each eye's display.
To ensure that consumers receive the best experience—and to establish their respective hegemonies—Oculus and Intel have each begun releasing their own "VR Ready" certifications. Last year, Oculus released its minimum specs for an acceptable VR experience. The first Oculus Rift-PC bundles rolled out a month ago, at prices that begin at $1,500. That might be tough for consumers to swallow, but those are the sort of prices that propped up the PC industry for years.
We often talk about VR devices, like the Rift, and AR devices, like the HoloLens, in the same breath, but the two are very different things.
VR headsets are more like external displays, with some intelligence inside them to track where a user looks; they're powered and driven by a desktop PC. AR devices, like Microsoft's HoloLens, roam without a power cord, but they place all their computing power—as well as a battery—on the user's head.
VR will remain the domain of the desktop gaming PC, repurposed for VR.
Of course, this bifurcation is nothing new to the PC industry, which has built portable laptops and more powerful desktop workstations for years. Some believe that AR devices will evolve like laptops, with an emphasis on mobility and battery life, while reserving their limited compute power for the handful of virtual objects the AR environment demands. VR headsets, on the other hand, will have the horsepower to render a complete detailed virtual landscape, but chances are you'll be sitting at your desk or couch to enjoy it.
CPU and GPU vendors aren't saying yet if they'll develop optimized VR chips, or simply adapt what they already have. And it's unclear whether headsets will sport a traditional X86 chip or a mobile chip like Qualcomm's Snapdragon. Naturally, other mobile technologies, like the 4K displays built into phones like the Samsung Xperia Z5 Premium, make sense: When a display is strapped three inches from your eyes for possibly hours, you're going to want the best available.
Intel's Soqui and representatives from other chip makers say they see AR and VR technologies eventually meeting in the middle. We're already seeing signs of that, as with the HTC Vive, which includes basic AR capabilities. Intel's vision goes further: Soqui says Intel believes it can eventually "tether" a VR device to a PC by streaming gobs of data across a wireless link—even knowing that latency has to be avoided at all costs.
Whether it be AR or VR, the future of the industry is a physically untethered experience.
How will Intel do that? Soqui declined to comment. But Intel has already launched a wireless dock that supports the new 802.11ad WiGig standard, which can stream a whopping 7Gbps over short distances. Intel and Qualcomm also recently announced interoperability between their respective 802.11ad chipsets. Intel's goal for "wire-free" PCs has been a little aggressive, but the company believes in the mission enough to build 802.11ad support into Skylake PCs. VR makes the argument for such support even stronger.
The only problem: 802.11ad uses 60GHz technology, which can't really penetrate walls. An "untethered," wireless VR solution, therefore, will likely require a broadcast point in the same room.
VR is surprisingly mature for an industry that hasn't even actually launched. There's a "free" option: Google Cardboard, which has even been available in a box of breakfast cereal. There's a convenient distribution method: The Vive, co-developed by HTC and Valve software, delivers software via Steam codes. Another 40 or so experiences, apps, and games are available to try out for the Rift.
And brands love VR, too. Chuck Peil, head of business development and partnerships at ReelFX, said he was aware of about 30 pieces of VR content that companies like Lucasfilm, American Express, and others had either commissioned or were working on. There's even a rivalry between the two leading VR camps: Vive and Rift. Jean-Michel Blottiere, executive director of an animation conference at Germany's Filmakademie Baden-Wurttemberg, said that developers interested in telling a story seem to be leaning toward the HTC Vive, favoring the freedom that the headset allows within a virtual space.
What all this means is that there should be a viable ecosystem of apps and content, enough to help keep early VR adopters interested. As products like Microsoft's Lumia smartphone have shown us, without apps, users will wander off.
Sony may have launched—and quickly sold out of—its PlayStation VR preorders, but the PC seems to be well-positioned to capture the market. That's because consoles like the PlayStation 4 are already several years old, while PCs can be constantly refreshed.
Sony's PlayStation VR depends on the console to power it. Over time, the PC will gain more and more processing power, making it an attractive alternative.
It's also the sort of challenge that has the PC industry smacking its lips. Of late, the PC industry has put forward a tired old argument that says hundreds of millions of PCs are five years old, and PC owners really ought to upgrade with new components. With VR, this argument becomes more compelling since it means a customer can actually do something new with his or her machine.


text:
Precinct analysis: None of the above
We have been told that this was a year where many people were unhappy with the two main choices they had for President. We looked at Presidential numbers in Harris County before, and now we're going to look again, at write-in candidates and at undervotes.
Dist McMullen  All WI  McMullin%  All WI%
HD126     354     417      0.57%    0.67%
HD131      63      87      0.14%    0.19%
HD137      89     100      0.32%    0.36%
Dist     None   Total   None %
HD126   1,349  63,214    2.13%
HD128     909  60,656    1.50%
The first table documents the votes for Evan McMullin, who drew by far the most votes among the thirteen certified write-in candidates, which means the thirteen whose votes were actually counted. The second column is for all write-in votes for the given district. There were 6,510 total write-in votes, with McMullin receiving 5,647 of them. To put that in some perspective, Ralph Nader received 1,716 write-in votes in 2004, for 0.17% of the vote. McMullen had 0.43% of the vote, a hair less than half of Jill Stein's 0.90% share.
Not surprisingly, McMullin drew most of his votes in heavily Republican districts. That's no doubt because McMullin ran as a viable alternative for Republicans who were unhappy with Trump, and because there were more Republicans in those places. The two districts that stand out here are HDs 128, the only Republican district where McMullin finished below his countywide percentage, and 146, the only Democratic area where he outperformed the overall number. My guess for HD128 is that the voters there were just happier with Trump than voters elsewhere. As for HD146, I got nothing. Feel free to speculate about that in the comments.
The second table is for undervotes, which is to say the people who did not vote in the Presidential race. As you might imagine, that is usually the race that has the lowest undervote rate. This year, the undervote rate in the Presidential race was 1.99%; the next lowest rate was in the Tax Assessor's race, where 3.47% skipped it. County judicial races were around five percent. Before I talk about the rates in each district, here's how the Presidential undervote compared to other years:
Year   Undervote   Under%
2016      26,622    1.99%
Gotta say, I would not have expected 2004 to have had that many undervoters. I don't see much of a pattern here. HD128 again demonstrated its satisfaction with the candidates by having the lowest undervote rate, but the districts that gave McMullin the most support did not necessarily have high undervote rates. Both Democratic and Republican districts above average and below average. Maybe you see something there, and maybe if I went down to the precinct level I'd see something, but right now I don't. It just is what it is.
I'm going to take a crack at Fort Bend and Dallas Counties next week. As always, let me know what you think.
The Harris County GOP thinks it can come back in 2020
As goes Tarrant
Precinct analysis: Ogg v Anderson
Tagged: Donald Trump · Election 2004 · Election 2008 · Election 2012 · Election 2016 · Evan McMullin · Harris County · HD128 · HD146 · precinct analysis · President · Ralph Nader · write-in candidate
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