Blockchain Papers

Alexandre Tran, David Granton, Eddy Fan, Bram Rochwerg

Clinical practice guidelines (CPGs) are used by critical care clinicians to guide practice and inform best care. According to the GRADE framework, evidence synthesis should preferentially rely on randomized controlled trials (RCTs) because they minimize bias and establish causality.1 Despite challenges, critical care is well-suited to randomized studies given its (1) high incidence of acute conditions, (2) protocolized interventions, (3) standardized outcomes, and (4) strong data infrastructure and trial networks.2,3 Despite the advantages, RCTs are often unavailable for CPGs or leave knowledge gaps, particularly for subgroup effects or patient-important outcomes like long-term quality of life related to heterogeneous populations, urgent interventions, and recruitment constraints.4,5 Physicians may hesitate to apply RCT results because (1) enrolled patients differ from real-world populations, (2) key outcomes may be unmeasured, (3) effect estimates may be imprecise, and (4) subgroup analyses may be lacking.6 When RCT evidence is insufficient, high-quality non-randomized studies of interventions (NRSI) can complement trials by approximating causal inference—estimating exposure effects while separating systematic bias from random error.7 High-quality NRSI ­require large, well-validated datasets with minimal missingness and adequate temporal resolution. Without these, even advanced analytics cannot yield credible estimates. NRSI often emulate target trials, aligning eligibility, time zero, and predefined interventions and outcomes.8,9 Design must reflect strong knowledge of confounders and time-varying biases, addressed through advanced data and statistical methods. When based on explicit and credible assumptions (eg, exchangeability, no residual confounding), NRSI can yield valid and generalizable estimates, though such assumptions cannot be proven and still require caution in interpretation.10 Most NRSI are retrospective and lack safeguards standard in RCTs such as trial registration or prespecified outcomes. In target-trial emulation (Table 1), preregistration before data access is critical to prevent selective reporting and analytic flexibility, mirroring RCT practice. These limitations are especially relevant in critical care, given dynamic physiology, urgent decisions, and substantial clinical heterogeneity. These factors complicate exposure timing, increase time-varying confounding, and challenge stability assumptions in target-trial designs. Rigorous cohort definition and analytic strategy are essential when applying NRSI in this context. As causal-inference methods such as target-trial emulation spread, cautious application with methodological rigor and transparency is essential to avoid poorly executed, misleading, or irreproducible NRSI. High-quality NRSI depend not only on analytical sophistication but also on careful data acquisition, explicit protocolization, and transparency in prespecifying exposures, outcomes, and analytic plans—principles that mirror RCT standards. Target trial (ideal RCT) versus emulation. 1. Treatment with ECMO therapy if PaO2/FiO2 < 80 mmHg 2. Treatment with conventional mechanical ventilation without the use of ECMO therapy Adapted from: National Academies of Sciences, Engineering, and Medicine; Health and Medicine Division; Board on Health Care Services; Committee on Developing a Protocol to Evaluate the Concomitant Prescribing of Opioids and Benzodiazepine Medications and Veteran Deaths and Suicides. An Approach to Evaluate the Effects of Concomitant Prescribing of Opioids and Benzodiazepines on Veteran Deaths and Suicides. Washington (DC): National Academies Press (U.S.); 2019 Sep 24. 2, Specifying the Target Trial. Available from: https://www.ncbi.nlm.nih.gov/books/NBK547516/. Case example: Venovenous extracorporeal membrane oxygenation in patients with acute covid-19 associated respiratory failure: comparative effectiveness study.22 This commentary examines the evolving role of NRSI in developing critical care CPGs. We outline key challenges in conducting and synthesizing critical care research, then describe how high-quality NRSI can complement randomized evidence by (1) aligning effect estimates with RCTs, (2) informing certainty of evidence (CoE), and (3) guiding clinical practice recommendations. We propose practical strategies for CPG panels and domain experts to maximize the utility of NRSI while maintaining methodological rigor. Our goal is to support CPG panelists, researchers, and clinicians in interpreting recommendations that integrate NRSI. These recommendations align with evolving GRADE guidance, operationalizing its principles for critical care applications. GRADE provides a structured approach for rating CoE, the confidence that an estimated effect is close to the truth.11 When ­developing guidelines, the GRADE Evidence-to-Decision (EtD) framework translates synthesized evidence into recommendations by weighing intervention effects, CoE, patient-valued outcomes, and contextual factors such as resource use, equity, acceptability, and feasibility.12 These contextual judgments ensure that evidence is interpreted through a patient- and system-centered lens, recognizing that even high-certainty data require value-based consideration before adoption into practice. A review of critical care CPGs showed reasonable uptake of GRADE, with recommendation strength generally aligned with CoE.13 However, strong recommendations are still often made from low or very low-certainty evidence, often related to evidence gaps in RCTs. This highlights the need to integrate high-quality NRSI into CPG development to strengthen evidence synthesis and uptake. Critical care CPG panels should consistently apply GRADE principles, incorporating all high-quality evidence, including NRSI to augment situations where RCT data may be limited or absent. RCTs are resource-intensive and difficult to conduct in critical care.1 To maintain feasibility, investigators often overestimate effect sizes, leading to underpowered studies that may miss true effects.14,15 Reviews of critical care RCTs show that predicted treatment effects are often exaggerated—nearly 10-fold higher than observed, and that few trials sufficiently justify their sample-size targets.16 Similar overestimation has been reported in sepsis, stroke, and trauma trials.17–19 Among high-profile publications, fewer than half of trials had reproducible results.20 Moreover, a meta-epidemiologic review of more than 600 critical care trials found that only 1 in 16 was at low risk of bias, with little improvement over 4 decades.21 These findings suggest that RCTs alone may not provide sufficient high-quality evidence to inform strong guideline recommendations. Critical care populations are highly heterogeneous, encompassing subgroups with different baseline risks and treatment ­responses. RCTs often target broad syndromes such as sepsis or acute respiratory distress syndrome (ARDS), which likely contributes to many “negative” trials unable to detect differences in outcome.22 Because these studies estimate average treatment effects (ATEs) across diverse patients, potential subgroup benefits can be obscured when other subgroups experience harm.23 This variability, termed heterogeneity of treatment effect (HTE), reflects non-random differences in benefit or harm linked to patient characteristics.24 Understanding HTE (Table 2) is central to precision medicine: treatments that appear neutral on average may conceal offsetting benefit and harm across biologically or contextually distinct subgroups. Explicit exploration of these differences can refine trial design, improve interpretation, and guide targeted recommendations. Methods for assessing heterogeneity of treatment effect. Case example: Heterogeneous treatment effects of therapeutic-dose heparin in patients hospitalized for COVID-19.19 Causal forest and other machine-learning approaches allow for non-linear and interactive modeling of treatment effect heterogeneity but are more susceptible to overfitting and typically require larger sample sizes and external validation. In contrast, regression-based risk modeling approaches are generally more interpretable but may oversimplify interaction effects. RCTs typically assess HTE using pairwise subgroup analyses, but these are often underpowered, rely on arbitrary subgroup thresholds (eg, age <65 vs ≥65), and cannot capture complex interactions.25 The American Thoracic Society (ATS) and European Respiratory Society (ERS) guideline on non-invasive ventilation illustrates these limitations: subgroup evidence for conditions such as acute hypoxemic respiratory failure or ARDS came mostly from small or secondary analyses, yielding sparse data and very low certainty.26 These challenges highlight the need for improved data science approaches to identify and characterize HTE: a priority emphasized in the recent ATS research agenda for sepsis and ARDS.27 Data-driven subgroups (subphenotypes) can integrate multiple patient characteristics to assess effect modification and estimate individualized treatment effects.28,29 These models require rigorous derivation and validation to avoid overfitting, yet no consensus framework currently guides their validation or clinical use. Critical care trialists should adopt realistic effect size and recruitment targets and predefine strategies to evaluate clinically relevant HTE. When RCT evidence is insufficient, we propose strategies for CPG panels to integrate NRSI within the GRADE framework to complement RCTs and strengthen recommendations. In accordance with GRADE guidance, if the CoE from RCTs is judged to be high then the role for NRSI is minimal for the specific comparison and outcome of interest.7 However, RCTs often do not report certain patient-important outcomes such as adverse events, quality of life, or longer-term morbidity or mortality. Even if a particular question and outcome of interest have RCT evidence, the estimates of treatment effect are often limited by imprecision due to aforementioned recruitment and sample size concerns. Treatment effects are often assessed in highly selected populations; trial participants typically represent a small fraction of those screened and even meta-analyses may yield low certainty due to imprecision or inconsistency.30,31 In these situations, guideline panels should consider high-quality NRSI, defined by adherence to TARGET (Transparent Reporting of Observational Studies Emulating a Target Trial) standards, acceptable risk of bias, and robust sensitivity analyses, to supplement RCT evidence.7 Target-trial emulation exemplifies this approach: investigators first design a hypothetical randomized trial addressing the question of interest, then emulate it using observational data.8,32 For instance, an international study using the COVID-19 Critical Care Consortium dataset estimated the effect of VV-ECMO versus conventional ventilation in patients with severe COVID-19, providing real-world evidence where an RCT was impractical due to complexity and cost.33 Similar emulations have evaluated intubation,34 ventilation,35 and corticosteroid strategies36 in critical care—demonstrating how NRSI can inform practice when trials are unfeasible. Consider the example of drotrecogin alfa (activated protein C, rhAPC). Following the PROWESS RCT,37 which demonstrated benefit of rhAPC in patient with septic shock, the large open-label ENHANCE observational study38 reported a similar reduction in mortality with rhAPC but was the first to raise important concerns about serious bleeding, including intracranial hemorrhage. These observational findings influenced early guideline discussions, tempering enthusiasm for the drug, and subsequent RCTs39,40 confirmed this harm and rhAPC was ultimately withdrawn. This highlights that replication across larger datasets remains essential to confirm findings and ensure generalizability beyond selected RCT populations. This sequence illustrates an iterative process: observational signals can generate early warnings or hypotheses that subsequent RCTs confirm or refute. When results diverge, these contrasts can highlight methodological limitations or context-specific factors that warrant further investigation. The TARGET statement outlines 21 reporting items to standardize eligibility, interventions, outcomes, and analyses, improving transparency and reproducibility of emulated trials.41 Adherence to TARGET helps guideline panels assess NRSI rigor and determine when such evidence can complement or upgrade certainty around RCT findings. Similarly, the RCT-DUPLICATE initiative evaluated whether database-derived emulations can reproduce findings from RCTs across 32 cardiovascular studies, including interventions for anticoagulation, antiplatelet therapy, and chronic disease management. The authors found that effect estimates from well-designed emulations closely mirrored their RCT counterparts in both direction and magnitude, demonstrating that real-world data can yield valid causal inference when study design and analytic methods are rigorous.10 Whether successes from other fields will translate to critical care remains uncertain, given its confounding, physiologic complexity, and HTE. A blinded target-trial emulation in this setting reproduced findings of the PreVent RCT examining bag-mask ventilation and hypoxemia,42,43 providing proof-of-principle that short-term physiologic effects can be predicted from observational data, though its value for longer-term or patient-centered outcomes remains untested. Valid causal inference in NRSI requires adherence to key assumptions: exchangeability (no unmeasured confounding), positivity (each patient could receive any treatment), and consistency (observed outcomes reflect potential outcomes under that treatment).8,9 Meeting these assumptions demands careful cohort design, proper time alignment, and analytic techniques that address confounding, such as target-trial emulation, inverse-probability weighting, or doubly robust estimators.44,45 Studies must also handle time-varying confounding and competing risks (eg, death precluding extubation), which can otherwise bias effect estimates.46 To address these concerns, marginal structural models may be used to estimate the causal effect of a time-varying treatment and address the challenge of estimating treatment effects when confounders are influenced by prior treatment—a situation conventional regression models struggle with. CPG panels should systematically appraise NRSI by verifying TARGET adherence, assessing bias with validated tools such as ROBINS-I, and judging how results affect GRADE domains such as imprecision, inconsistency, and indirectness.41,47 Robust sensitivity analyses, testing alternative models, handling missing data, and probing unmeasured confounding, are essential to confirm result stability and should be clearly reported.48,49 Transparent presentation of assumptions and their plausibility further strengthen credibility. When high-certainty RCT evidence already exists for all relevant target populations, additional NRSI are seldom needed (Figure 1). More often, however, critical care trials involve highly selected populations, making complementary NRSI useful for confirming ­treatment effects in broader or under-represented groups.50,51 When RCT and NRSI results are consistent, guideline panels may consider upgrading certainty and recommendation strength in line with GRADE guidance.7 GRADE also allows rating up observational evidence when large effects, dose-response relationships, or confounding that would only diminish an observed benefit are present.52 Conversely, inconsistent or methodologically weak NRSI such as those with implausible assumptions, poor reporting, or critical bias, should be excluded, with the rationale documented. Expanding use of target-trial emulation is promising but must be paired with training and standards to prevent low-quality proliferation that could erode confidence in observational evidence.48 Framework for incorporating NRSI into critical care CPGs. CPG panels should incorporate well-conducted NRSI to strengthen CoE and adopt structured workflows: (1) verifying TARGET adherence, (2) considering potential risk of bias, and (3) linking NRSI results to GRADE domains to ensure transparent, reproducible use of observational evidence. Critical care RCTs often study heterogeneous syndromes using strict eligibility criteria that limit generalizability and obscure subgroup effects. A multicenter simulation of 15 landmark trials found that over half of real-world ICU patients would have been ineligible,53 and a review of 75 high-impact trials showed that 60% used at least one poorly justified exclusion such as language barriers or lack of insurance—further restricting applicability.54 Most RCTs originate from high-income countries, leaving major evidence gaps for critically ill patients in the Global South.55 For example, a Zambian sepsis RCT found higher mortality with early fluid resuscitation—contradicting prior goal-directed therapy trials.56,57 This discordance may be explained by the fact that these trials enrolled predominantly young, malnourished individuals predisposed to pulmonary edema and respiratory failure in a setting with limited ventilatory support. Beyond generating estimates of effectiveness in underrepresented populations, NRSIs also offer a pathway to address structural inequities in evidence generation and utilization. Conducting RCTs in the Global South is often hindered by logistical, regulatory, and infrastructural challenges—including limited research infrastructure, ethical oversight, or funding mechanisms, which systematically exclude these populations from RCTs.55 Well-designed NRSI can help bridge such gaps by leveraging local data to assess effectiveness, feasibility, and contextual factors in resource-limited settings. They can also identify structural and contextual modifiers such as malnutrition, health-system capacity, and disease epidemiology; thereby supporting more equitable, context-specific guideline recommendations.58 Embedding such evidence from the Global South not only broadens external validity but also enhances the global relevance of CPGs—thereby promoting more equitable and relevant evidence-based decision-making for clinicians practicing in resource-limited settings. NRSI can also inform feasibility, acceptability, and which are key factors in CPG For instance, the ATS guideline on ARDS a recommendation for VV-ECMO based on NRSI substantial in and across and NRSI can RCT findings to real-world which patients benefit or are based on risk or A key is which to assess how RCT results to external populations and to identify contextual effect improving both evidence relevance and trial Causal inference using real-world data can evaluate HTE across broader populations, including and patients typically underrepresented in a systematic review found major in methodological rigor for HTE analyses, particularly in testing and for confounding, the need for standardized methods and In critical care, HTE from secondary analyses of RCT In the modeling showed that patient characteristics predicted benefit from specific oxygenation targets for patients with and higher for those with The subsequent Care Medicine a recommendation higher oxygenation targets based on very low-certainty an of the trial found that even when are machine-learning models can identify clinically subgroups with benefit or the value of HTE modeling in acute respiratory These secondary analyses are and but should be by observational studies to evaluate HTE beyond RCTs. The ARDS cohort illustrates the value of non-randomized showed that patients had mortality with higher while no benefit in the example of HTE using real-world ICU Beyond also a global of guideline adherence, and ARDS outcomes. not its and rigor how observational studies can yield at a RCTs informing international ARDS When developing panels should consider how best to incorporate NRSI in HTE. this requires systematically HTE analyses, particularly for subgroups in the and assessing how these findings complement subgroup no GRADE yet panels should still evaluate whether HTE evidence recommendations or can guide research for or in RCTs. CPG panels should apply well-conducted causal-inference analyses to confirm the generalizability of RCT findings and identify clinically important HTE. RCTs the standard for and but well-designed NRSI can augment both the certainty and of evidence. Critical care CPG panels should integrate observational evidence when while recognizing methodological standardized (1) TARGET for reporting, (2) validated risk of bias and (3) explicit GRADE will ensure use of NRSI across guideline High-quality NRSI can CoE and generalizability beyond selective RCT populations, providing a to evaluate HTE. incorporating such studies into CPG development may improve both the generalizability and of recommendations. such as the dataset highlight how NRSI can HTE not in trials As analytic methods and target-trial NRSI will an important role in addressing evidence gaps in critical care. will rely on close across and to ensure that NRSI are and with the rigor of randomized authors the the authors to the and of the is at American of and Critical Care Medicine the which have been as tools used in this

Henrik Axelsen, Johannes Rude Jensen, Omri Ross

Decentralized Autonomous Organizations (DAOs) have seen exponential growth and interest due to their potential to redefine organizational structure and governance. Despite this, there is a discrepancy between the ideals of autonomy and decentralization and the actual experiences of DAO stakeholders. The Information Systems (IS) literature has yet to fully explore whether DAOs are the optimal organizational choice. Addressing this gap, our research asks, "Is a DAO suitable for your organizational needs?" We derive a gated decision-making framework through a thematic review of the academic and grey literature on DAOs. Through five scenarios, the framework critically emphasizes the gaps between DAOs' theoretical capabilities and practical challenges. Our findings contribute to the IS discourse on blockchain technologies, with some ancillary contributions to the IS literature on organizational management and practitioner literature.

Germán Fierro

Arterial hypertension affects a third of the world's population and is a significant risk factor for cardiovascular disease. Blood pressure (BP) is one of the most relevant parameters used for monitoring of possible hypertension states in patients at risk of cardiovascular disease. Hence, there exists a need for new monitoring solutions, which allow to increase the frequency between BP assessments, but also allow to reduce the level of occlusion in the attempts. Moens-Korteweg equation is among the main principles to estimate BP by dispensing of any inflatable cuff. This principle might lead to an indirect estimation of BP by measuring the time it takes the pressure pulse to propagate between two pre-established vascular points, accordingly the pulse transit time (PTT) method. This thesis proposes a wearable PTT-based method to estimate central aortic BP (CABP) and, the main milestones of this work included: proof of concept of the proposed method (pilot work), the development of a wearable device (including two stages of validation), the proposition of a miniaturized version (integrated circuit) of the analog front-end of the wearable hardware, and, the development of a novel PTT-based model (PTTBM, i.e., the mathematical relationship between measured variables and estimated BP) suitable for the proposed wearable methodology to estimate BP. The main contributions found at each milestone are presented. One of the contributions of this thesis is the use of the PTT-principle for estimating CABP instead of the peripheral BP (PBP) (as typically used in the literature). The pilot work showed the feasibility of CABP estimation from the PTT principle by using electrocardiogram (ECG) and ballistocardiogram (BCG) recordings from off-the-shelf equipment. Results showed that CABP was more correlated with the proposed methodology in comparison to all PBP variables assessed; confirming our hypothesis that the CABP is the most suitable parameter to collate through the time elapsed from ECG R-wave to the BCG J-wave. That is, considered featured time (RJ-interval) includes the time of a pulse pressure propagating at an aortic district. Bland-Altman plots showed an almost zero mean error (\u\ < 0.02mmHg) and bounded standard deviation o < 5mmHg for all systolic and mean central BP readings. Pilot work provided a landmark in order to develop a compact device that allows the integration of wireless blood pressure monitoring into a wearable system. Another contribution of this thesis is the proposition of a wearable device for PTT-computing by also including design considerations for the signal conditioning chains for ECG and BCG signals. The proposed design procedure takes care of minimizing the impact of spurious delays between physiological signals, which eventually degrade the PTT computation. Further, such a procedure could be suitable for any PTT-acquisition. Filtering with low and controlled delay is required for this biomedical application, and proposed conditioning chains provide less than 2ms group-delay, showing the effectiveness of the proposed approach. In order to provide the methodology with higher autonomy and integration, a highly miniaturized implementation of the filtering approach was also proposed. It includes the design of proposed architectures in CMOS technology to implement the particular low-delay filtering at reduced bandwidth featuring ultra-low-power characteristics. Results show that less than 2ms delay for the ECG QRS-complex can be achieved with a total current consumption of IDD = 2:1nA at VDD = 1:2V of power supply. Such development meant another significant contribution of this work in the conception of highly autonomous wearable devices for PTT acquisition. The first stage of validations on the wearable CABP estimation showed that, when considering data from one volunteer, results achieved with off-the-shelf equipment could be replicated by using a proposed wearable device, and the method could be further validated by using the wearable version. Additionally, CABP estimation from the proposed wearable device could be feasible by using three feature times (FTs) as CABP surrogates; that is, RI, RJ, and IJ intervals (from ECG and BCG wearable recordings). The first validation of the method also showed that CABP could be accurately predicted by the proposed methodology when in the order of daily calibrations are performed. The second stage of validations involved a study with a group of volunteers, and new alternatives were explored (twentyseven: nine PTTBMs along the three FTs) for the CABP estimation. We found that CABP could be accurately estimated (inside AAMI requirements) through the presented methodology by using four of the explored alternatives, whereas the RI interval, an FT lacking any PTT assessment, emerged as the best surrogate for the CABP estimation. Hence, a principle different from the traditional PTT-based method arises as a more advantageous method for the CABP estimation in the light of evidence reported in this validation, and, to our knowledge, this is the first time that CABP has been successfully estimated from a wearable device. The final significant contribution of this thesis meant the last chain-link in the process to achieve an utterly original method to estimate CABP. A novel PTTBM to estimate CABP is proposed, which uses a ow-driven two-element Windkesel network constructed from FTs extracted from the wearable recordings. When classic PTTBMs are applied, the fitting of parameters often leads to values without a physiological basis. Opposite to that in the proposed PTTBM, the parameters have a clear physiological meaning, and the parameter fitting led to values that are consistent with this meaning and more stable throughout calibrations. In conclusion, this thesis introduces a novel device that exploits an alternative and indirect method for CABP estimation. Variants of the principle used, accordingly, PTT method, have been previously explored to estimate PBP but not for central aortic BP. Additionally, the device was designed to be wearable; that is, it is attached to the clothes, causing low discomfort for the user during the measurement, thus, allowing continuous and ambulatory monitoring of aortic pressure. The developed wearable system, validated in a series of volunteers, showed promising results towards the continuous CABP monitoring.

J O'donnell

Although the problems identified in the statement have been known for several decades, previous expressions of concern and calls for action have not fostered broad improvements in practice.2 A P value of 0.05 carries a 5% risk of a false positive result (i.e. there is no true difference between treatments). If a trial is meant to provide proof of a genuine treatment difference beyond reasonable doubt, a much smaller P value – say p < 0. 001 – is required.5 We disagree ….that our statement… is erroneous. According to the null hypothesis, P < 0.05 will occur 5% of the time.6 No editorial corrigendum has appeared. A P-value is the area under the curve of a probability distribution defined by a mathematical model. The model, usually presented graphically, describes the expected distribution of a sample statistic around a central measure, the parameter or theoretical ‘true’ value, for example the population mean, μ. Under the central limit theorem, this would be the standard normal distribution of sample means generated by repeat sampling of a population variable of interest. The mean of the sample means would equal the ‘true’ population mean, μ. In medicine, it is rare for us ever to know the true value of the variable of interest. However, we can usefully assign a value in the special case of a difference statistic, for example the difference in mean outcome variables in a placebo-controlled drug trial. In this case, the sampling distribution would represent that of the difference statistic. In this case, if the value we assign μ is zero then the mathematical model becomes the null hypothesis used in NHST. By way of contrast, non-inferiority drug trials require a non-zero value to be assigned. The cumulative AUC of the sampling distribution of a continuous variable is represented by a mathematical function called the cumulative density function. In medical science, most study variables are continuous or, if categorical, are transformed using the logit model. As the P-value is a mathematical integral, that is the cumulative AUC, it cannot take on a precise value as there is no AUC defined by a single point on the curve, for example the P-value ≤ 0.05, but not P = 0.05. While this may seem pedantic, the semantics of statistical inference are influential in thinking and decision-making yet misinterpretation and misuse of terminology are commonplace. Under the null hypothesis, one sample mean that happens to fall within an extreme region of the standard normal distribution may be expected to occur with a low frequency, say P ≤ 0.05 meaning such a sample mean or one more extreme would be expected to occur with a frequency of 5% or less. To be valid, the assumptions of independence and random selection of each sample mean selected from the normal distribution of sample means must be assumed. Another way of stating this is as a conditional probability: . Note: | means ‘given’. It is important to understand that the P-value is a measure conditional on the assumption that the mathematical model describes the distribution of sample means and is not a measure of the probability of the ‘truth’ of the mathematical model. To make this claim would invert the conditional probability statement and commit an error of reasoning called transposing the conditional7 aka the prosecutor's fallacy: . In reasoning from NHST, the commonly used definition of the P-value as ‘a measure of evidence against the null hypothesis’ is potentially misleading in that it seems to legitimise transposing the conditional as if it were a mathematically valid function rather than a matter of intuition. It was the intuitive interpretation that Fisher used in his a posteriori model of NHST.8, 9 His aim was to use the P-value as an aid in deciding which experiments to repeat. If on several repetitions, a consistent extreme P-value for the sample statistic was obtained then that would accumulate evidence for a true experimental effect. If no such effect was present, regression to the mean parameter (μ) would be expected (P ≥ 0.05). In real-life scenarios, many factors inhibit repetition and replication of experiments; however, modelling can give us insight into the precision and reproducibility of extreme P-values10, 11 and hence the intuitive weight we place on the P-value ‘as a measure of evidence against the null hypothesis’. Table 2 is a reproduction.10 It describes the results of simulating repeat experimentation and the probability of producing a P-value ≤ 0.05 under the prescribed conditions of the simulated experiment. It may be surprising to many how poorly reproducible the P-value is as a bright line test (a bright line test is a clearly defined rule or standard, the purpose of which is to produce consistent and predictable results). For example, if in the first experiment P ≤ 0.05 was produced there would be a 50% probability of reproducing P ≤ 0.05 in a repeat experiment; if P ≤ 0.01was produced in the first experiment the probability of producing P ≤ 0.05 in a repeat experiment, would be 73%; and if P ≤ 0.001 was produced in the first experiment the probability of P ≤ 0.05 in a repeat experiment would be 91%. The magnitudes of a number of these first experiment P-values are those commonly used in pharmaceutical trials and other medical analyses. The P-value is also sensitive to sample size. Irrespective of the effect size, with increasing sample size (n) the P-value can be made as small as you wish12 because the standard error is proportional to the inverse of n. If statistical significance is substituted for ‘clinical significance’ even small irrelevant differences may be regarded as worthy of investment. Large sample sizes are often a feature of pharmaceutical trials of secondary and primary prevention interventions such as preventive therapies in atherosclerotic diseases and osteoporosis. The quoted extract from the article on clinical trials mistakenly promotes the P-value as a measure of error and further states that the error rate can legitimately be adjusted depending on the magnitude of the P-value thus providing ‘proof of a genuine treatment difference beyond reasonable doubt’. This erroneous interpretation has arisen from the illusion of coherence resulting from the conflation of the dominant models of hypothesis testing.8, 9 The setting of theoretical type 1 (α) and type 2 (β) error rates in the Neyman and Pearson model envisions the frequency of error ‘in the long run of experience’ (experimental repetition) given randomness and independence of sample means from two juxtaposed probability distributions. A priori two identical populations are imagined except that they differ in mean parameters, null μ0 and alternative μA. This model is valuable in providing a rationality to sample size selection. However, the conflation has resulted in confusion between Fisher's P-value and Neyman's α giving the P-value an apparent legitimacy as an a posteriori ‘sliding’ type 1 error rate. Even if this were logical, decreasing α would increase β, resulting in a decrease in power (1-β). Also the dichotomous approach of pitting null hypothesis against alternative hypothesis carries the risk of blinding the researcher or the consumer to other explanatory hypotheses. For those who think the use of confidence intervals (CI) overcomes the problems described, think again. Although it has greater intuitive value especially with respect to estimating effect size, the CI relies on the same premises as the P-value. For example the CI of juxtaposed probability distributions can be made as large or as small as can be paid for by increasing the sample size such that for any small difference the CI can be made not to overlap. Statistical analyses are very valuable tools for extracting information from data. However, the reliability of the knowledge generated is dependent on many more important factors inter alia, evidential justification of the experimental hypothesis, study design, study conduct and data collection and cleansing, competence in choice of statistical model, valid reasoning, reviewer bias, publication bias and replication. Much of the criticism of medical science centres on its overemphasis on the importance of the P-value, NHST and statistically defined effect sizes. A better understanding of how sound statistical inferences are made and how they influence decision making will be key elements to improving all aspects of healthcare. This is critically important in acknowledgement of individuals as complex adaptive systems with characteristics of emergence, adaptability, non-linearity and unpredictability13 rather than as static population averages. Surveys suggest statistical literacy amongst doctors is low.14, 15 Teaching and assessing knowledge and application of statistical inference, critical appraisal and decision-making skills should be a primary focus of medical schools and specialist colleges. Difficult concepts underpinning statistical inference may be more effectively and efficiently taught using computer simulation whereby the learner can manipulate effect sizes, sample sizes and other statistics in order to see how parameter estimates, P-values and CI change with reproduction and replication.16 This will foster a more in-depth understanding of the limits of statistical inference, making clinicians better able to choose wisely amongst the myriad of investigations and treatment options on offer. Subsequent to article submission and review the author attended the referenced ASA conference.2 A special issue of the ASA journal reporting the conference proceedings is planned for 2018. In the opening addresses, the 400 participants were encouraged to devote their energies to developing proposals and goals to address the long standing yet stubbornly persistent errors in statistical inference described in this article. While concrete proposals are yet to be endorsed by the ASA, many speakers emphasised the need to place greater emphasis on teaching the conceptual framework of the different philosophical approaches to science (mastering the concepts as a priority rather than the mechanics of statistical inference). The need for better understanding of statistical semantics on the part of non-statistician scientists was also highlighted. Further that the best way to achieve understanding would be to develop context-specific learning modules. An aspect of the conference that resonated with the author with respect to prediction in medical science was the idea that science defines degrees of uncertainty (not certainty) apropos caution must be applied to the use of prediction models in medical practice lest they be over-extended.

N. M. Gibbs, William M. Weightman

It is our contention that the authors of many clinical trials in anesthesia are not fully considering the implications of the minimum effect size of interesta entered in their power calculations, and are therefore making conclusions that are not supported by their findings. In this paper we use hypothetical examples to explain how the choice of minimum effect size of interest in the design of clinical trials sets conditions on their interpretation, including the threshold for clinical relevance, the magnitude of effect sizes that can be confidently excluded, and the discrimination between primary and secondary outcomes. We then use examples from a sample of recent highly cited anesthesia trials to show that this is a problem, which as a specialty we should be addressing. THE MINIMUM EFFECT SIZE OF INTEREST IN THE DESIGN OF CLINICAL TRIALS Let us suppose that a group of researchers wishes to investigate whether a new short-acting antihypertensive drug has a clinically worthwhile treatment effect for the attenuation of the arterial blood pressure response to tracheal intubation. The first step in planning their study is to estimate the sample size required to detect a clinically worthwhile difference for their primary outcome (in this case the blood pressure response), with adequate power.1–4 The alternative, using a confidence interval (CI) approach, is to predefine an acceptable CI width for the primary outcome.b5,6 After careful consideration of all factors, including drug costs, they decide that the minimum clinically worthwhile difference or “threshold for clinical relevance” is 10 mm Hg. This is their minimum effect size of interest. They perform a t test with a null hypothesis that there is no difference between the new drug versus control. They accept a type I error rate of 5% (α = 0.05; i.e., P < 0.05 will be considered significant), and a type II error rate of 20% (β = 0.2, i.e., power = 80% [power = the probability of getting a statistically significant result if there is a true difference ≥ the specified minimum effect size of interest]).1–4 They anticipate that the SD in both groups will be about 10 mm Hg. With these variables they require n = 16 in each group.7 (If they had chosen a minimum effect size of interest = 5 mm Hg, they would have required n = 63 in each group; alternatively, with n = 16 in each group, their power would be reduced to around 29%.)7 THE ROLE OF THE MINIMUM EFFECT SIZE OF INTEREST IN THE INTERPRETATION OF CLINICAL TRIALS Scenario 1: No Significant Difference In a hypothetical scenario, the authors find that the mean difference is 6 mm Hg (95% CI −0.4 to 12.4 mm Hg), P = 0.06. They accept (or more correctly, fail to reject) their null hypothesis and conclude that there is “no difference” between the groups. This conclusion is not correct. A nonsignificant finding does not support a conclusion of no difference without qualification.2–4,6 Nonsignificant findings are qualified by the minimum effect size of interest entered in the power calculation, and the power. This is because the minimum effect size of interest entered in the power calculation is also the “minimum detectable difference” of the trial.1–4 The trial does not exclude or confirm a difference up to this value (in this case 10 mm Hg). Moreover, the power (1 – β, in this case 80%) defines the likelihood of a type II error (β, in this case 20%). In other words, in this scenario there is still a 20% chance that there is a true difference ≥10 mm Hg, even though the investigators failed to find a statistically significant difference. This is very different from an unqualified conclusion of “no difference”! Moreover, while the null hypothesis may not have been rejected, the actual P value continues to provide important information about the probability of observing the finding (or one more extreme) given that the null hypothesis is true. For example, in this case the probability is 6%; in contrast, if the P value were 0.6 rather than 0.06, it would be 60%. Furthermore, the observed point estimate and its 95% CI remain the best estimate of the difference between groups, whether or not statistical significance is reached. For example, an observed 95% CI of −5.4 to 7.4 mm Hg would likewise have been “not statistically significant,” but would have suggested that the true point estimate is closer to 1 mm Hg, which would be very different than the actual example, where the most likely point estimate is about 6 mm Hg. The importance of the minimum effect size of interest and power when interpreting nonsignificant findings becomes clearer when we consider the possibility of smaller true effect sizes. For example, let us say that the drug cost turns out to be lower than expected and that most clinicians would accept a 5 mm Hg difference as clinically worthwhile, rather than the 10 mm Hg used by the authors. How then does the information from this trial help them in their decision whether to use the drug? The answer is very little. The trial was designed to have sufficient probability of detecting a difference, given that the true difference is ≥10 mm Hg. It provides little information on the probability of detecting a difference, given a true difference <10 mm Hg. Scenario 2: Significant Difference and Observed Effect ≥ Minimum Effect Size of Interest In another hypothetical scenario, the authors find a mean difference of 12 mm Hg (95% CI 0.5 to 23.5 mm Hg), P = 0.04. They reject their null hypothesis (acknowledging a 5% chance that they are making a type I error) and correctly conclude that there is a statistically significant treatment effect. They also correctly conclude that this treatment effect is likely to be clinically worthwhile, because the point estimate is at least as large as their predefined minimum clinically worthwhile difference (= minimum effect size of interest stipulated in their power calculation). Scenario 3: Significant Difference and Observed Effect < Minimum Effect Size of Interest In yet another hypothetical scenario, the authors find a difference of 6 mm Hg (95% CI 0.3 to 11.7 mm Hg), P = 0.04. They correctly conclude that there is a statistically significant treatment effect. But what should they conclude about whether the effect is clinically worthwhile? The hypothesis they tested was that there was no difference between the groups (null). The P value <0.05 supports rejection of this hypothesis. However, it does not provide information on the likely magnitude of the effect or whether it is clinically worthwhile. To assess whether the observed effect size is worthwhile, it is necessary to refer to the minimum clinically worthwhile difference decided before the trial began, and which was entered as the minimum effect size of interest in the power calculation (in this case 10 mm Hg). Therefore, the correct conclusion is that while there is a statistically significant effect in this particular trial (i.e., P < 0.05), the observed effect (6 mm Hg) is too small to be clinically worthwhile (i.e., <10 mm Hg). The authors may not accept this conclusion. They may argue that the 95% CI around their point estimate of 6 mm Hg includes 10 mm Hg, so their finding is still compatible with a clinically worthwhile difference. However, they would have to concede that the same 95% CI would be compatible with a range of effect sizes as small as 0.3 mm Hg, and that the true effect size is most likely closer to the point estimate of 6 mm Hg (i.e., <10 mm Hg). The authors may also argue that their original 10 mm Hg was not a true minimum clinically worthwhile difference, and was chosen only for pragmatic reasons to limit the required sample size. They may argue that 5 mm Hg is a more realistic value in any case. However, their trial did not have adequate power (i.e., only around 29%) to detect a ≥5 mm Hg difference.7 The authors may argue that the power is now irrelevant, because they have observed a statistically significant difference. This is a misconception, because there is no guarantee that a repeat trial with the same sample sizes would provide another significant result.8,9 The likelihood of reproducing a significant result (assuming that a true difference ≥ the stipulated minimum effect size of interest exists) is equal to the power of the trial.8 For example, with 80% power, if the trial were repeated using different samples of the same size, there would be an 80% chance of again observing a significant difference.8 In contrast, with 29% power, the likelihood would be only around 29%.8 It would be difficult to be conclusive about any finding with this low level of replicability. For this reason, the power of a study is important for both negative and positive findings. Reducing the minimum effect size of interest after the fact reduces the power, thereby reducing the likelihood of replicating a finding. In effect, the authors are faced with a dilemma. Either they accept that the observed effect size is too small to be clinically worthwhile, or they accept that they cannot be confident that the finding has >80% chance of being repeated. Neither of these supports a conclusion of a reproducible clinically worthwhile effect. THE MINIMUM EFFECT SIZE OF INTEREST AND PRIMARY VERSUS SECONDARY OUTCOMES Let us say the authors also assessed the heart rate (HR) response, but because this was a secondary outcome, they did not perform a power calculation. They found that the mean difference in HR was 6 beats per minute (bpm) (95% CI −1 to 13 bpm), P = 0.10. How should they interpret this finding? To interpret it correctly they need to refer to the minimum effect size of interest (= minimum detectable difference) in the power calculation and the power. Clearly, if these values are not presented, it is not possible to make a meaningful interpretation. Similarly, it would be difficult to interpret a P value <0.05, because without knowing the power and the minimum effect size of interest, it would not be clear how likely the result could be replicated.8,9 Unfortunately, it is not possible to extrapolate power from other outcomes.8,9 Moreover, it is not appropriate to perform a power calculation once the results are already known.6 The authors may argue that a power calculation is not necessary, because the CI alone provides sufficient information. This is another misconception. The CI does not provide sufficient information on the adequacy of the sample size, a major determinant of the CI width.5,6 Perhaps a larger sample size for the HR outcome (with the same sample variability) would have reduced the CI width around the same point estimate sufficiently for the lower limit to be above zero? In fact, ensuring an adequate sample size is equally important using CI as it is using inferential tests, as is predefining a clinically worthwhile difference.5,6 For these reasons, it is not possible to make conclusions about secondary outcomes, unless they are accompanied by this information.9,10 They might still be important (depending on the point estimate and the actual P value or the 95% CI), but remain as “observations” until confirmed or excluded in future studies.9,10 Nevertheless, let us say that in this particular trial the authors made conclusions about both blood pressure and HR responses without specifying which was the primary outcome. A quick check of the minimum effect size of interest would identify the blood pressure response as the primary outcome (i.e., the outcome for which the power had been calculated, the sample size estimated, and the threshold for a clinically worthwhile difference set).9 In this way the minimum effect size of interest discriminates between primary and secondary outcomes. A SAMPLE OF HIGHLY CITED ANESTHESIA TRIALS We identified 20 highly cited prospective anesthesia trials by interrogating the ISI Web of knowledge (http://apps.isiknowledge.com/, accessed December 2010) using the following search strategy: topic = anesthesia or anaesthesia; journal = Lancet, New England Journal of Medicine, Anesthesiology, Anesthesia and Analgesia, or British Journal of Anaesthesia; year of publication = 2001 to 2010, with ranking of trials by number of citations.11–30 Publications other than prospective clinical trials were excluded. We scrutinized the top 20 most cited trials for conclusions that were not supported by the minimum effect size of interest stipulated in their power calculations. We did not recheck any statistical analysis or assess any other aspect of the trials. Conclusions Based on Secondary Outcomes There were 10 trials that based 1 or more conclusions on secondary outcomes (for which no minimum effect size of interest or power was provided) (Table 1).15,17,18,21,22,24,27–30 Three trials even included the findings of a secondary outcome in their title (Table 1).15,17,27 In many cases, it was not possible to differentiate between primary and secondary outcomes without reference to the minimum effect size of interest in the power calculation.Table 1: Studies that Include Secondary Outcomes in Their ConclusionsConclusions Based on Statistically Significant Findings too Small to Be Clinically Worthwhile There were 5 trials with statistically significant findings for their primary outcome, but with an observed effect size less than their minimum effect size of interest (Table 2).13,17–19,30 For example, Myles et al. chose a minimum effect size of interest of 0.9% “because uptake into routine practice would require convincing proof of benefit.“13 Yet they observed a mean effect size of only 0.74%.13 Similarly, Carli et al. specifically chose a “minimum effect size of interest” of 36 m walked in 6 minutes, because this difference produced “a meaningful impact” on long-term exercise capacity.17 Yet they observed a mean difference of only 33.6 m at 3 weeks, and 18 m at 6 weeks.17 Neither Myles et al. nor Carli et al. concluded that their observed effect was too small to be clinically worthwhile. Similar considerations apply to the other 3 trials in this category (Table 2).18,19,30 Only Myles et al. presented the 95% CI for their observed effect size. The remainder either presented no CI for the observed effect size, or presented CI in a different metric to the minimum effect size of interest (Table 2).Table 2: Studies with a Statistically Significant Primary Outcome but an Observed Effect Size Less than the Minimum Effect Size of InterestConclusions Based on Nonsignificant Findings—Unable to Exclude All Clinically Worthwhile Effect Sizes Four trials had nonsignificant findings for their primary outcomes (Table 3).11,22,26,27 Scrutiny of their minimum effect size of interest indicated that none could confidently exclude all clinically worthwhile effect sizes. For example, they were powered to detect differences in the incidence of morbidity and mortality ≥10%, length of stay ≥2.5 days, awareness incidence ≥0.9%, and block success rate ≥23%, respectively. Yet effect sizes below these ranges might still be considered clinically worthwhile. (e.g., mortality and morbidity reduction of 9%, length of stay reduction of 2 days, incidence of awareness reduction of 0.8%, block success rate improvement of 22%). Only Rigg et al. explained that they could not confidently exclude the possibility of a worthwhile true effect size less than the minimum effect size of interest stipulated in their power calculation.11 Only Avidan et al. presented the 95% CI for their observed effect size (which was instead of a P value from an inferential test).26Table 3: Studies with Nonsignificant Findings for the Primary OutcomeConclusions Based on Findings with no Power Analysis or Stipulation of Minimum Effect Size of Interest There were 4 trials with no power calculation or minimum effect size of interest for any outcomes.12,16,23,25 None of these explained that their findings could not be fully interpreted without this information. CONCLUSION To fully interpret a clinical trial in which inferential statistics are used, it is necessary to go beyond effect size, and consider also the minimum effect size of interest stipulated in the power calculation. This is an important value, which not only has a major influence on the required sample size, but also defines the threshold for clinical relevance for positive findings, and the minimum detectable difference for negative findings (Fig. 1). Readers should also scrutinize the value chosen by the authors, to determine if it is appropriate. Failure to consider the minimum effect size of interest may result in erroneous conclusions, such as conclusions based on secondary outcomes, on outcomes that are statistically significant but not clinically worthwhile, or on nonsignificant findings that do not exclude the possibility of a smaller, but nevertheless true clinically worthwhile treatment effect. We have provided examples of such conclusions in a sample of highly cited anesthesia trials in a selection of high-impact-factor journals. Given their criteria for selection, it is unlikely that these trials represent a negatively biased sample in terms of quality of statistical reporting. We suspect that similar findings would be found in any sample of anesthesia trials. To address this situation, we recommend greater rigor in the design and interpretation of clinical trials, with closer scrutiny of the minimum effect size of interest (by both authors and readers), adequate power, and a focus on primary rather than secondary outcomes. For key secondary outcomes, we recommend that additional a priori power calculations be provided, along with their minimum effect sizes of interest. The use of CI for the observed effect size has advantages, because CI provide information on the most likely true effect size and the range of likely true effect sizes for both primary and secondary outcomes. Nevertheless, the same principle of defining the minimum clinically worthwhile effect size before the trial commences applies, as well as holding to this value when interpreting outcomes, and ensuring that an adequate sample size was used.Figure 1: The central role of the minimum effect size of interest in the design and interpretation of clinical trials. Once chosen, the minimum effect size of interest determines the sample size required (for any given level of power, α, and sd of the samples). The threshold for clinical relevance for the observed effect size and the minimum effect size detectable (given the power) are mathematically equal to this value. As sample size cannot be changed once the trial is completed, none of the values can be altered post hoc without affecting the trial's power.DISCLOSURES Name: Neville M. Gibbs, MD, FANZCA. Contribution: Study design, conduct of study, data analysis, and manuscript preparation. Name: William M. Weightman, MB, FANZCA. Contribution: Study design, conduct of study, data analysis, and manuscript preparation. This manuscript was handled by: Franklin Dexter, MD, PhD.

Frank C. Day, David L. Schriger

Discussion Points1Cruz et al1Cruz C.O. Meshberg E.G. Shofer F.S. et al.Interrater reliability and accuracy of clinicians and trained research assistants performing prospective data collection in emergency department patients with potential acute coronary syndrome.Ann Emerg Med. 2009; 54: 1-7Abstract Full Text Full Text PDF PubMed Scopus (13) Google Scholar contains 2 parts, a comparison of the values gathered by trained research assistants and physicians about historical information in chest pain patients and the comparison of these participants' recordings with a “correct” value for each item.A. For each part, indicate whether the authors are studying reliability or validity and explain the difference between these concepts.B. What did the authors use as their criterion standard for the validity analysis?C. What are potential problems with their method of defining the criterion (gold) standard? Can you think of alternative approaches?D. The authors report crude agreement and interquartile range for their validity analysis. What part of a distribution is described by the interquartile range? List other statistics used to describe the validity of a measure and why they might be preferable to reporting crude agreement.2Tabled 1MD Recorded “Yes”MD Recorded “No”TotalRA recorded yes1176123RA recorded no18220Total1358143MD, Medical doctor; RA, research assistant. Open table in a new tab A. Calculate the crude percentage agreement for this table. What is the range of possible values for percentage agreement?B. Calculate Cohen's κ for this table. What is the formula for κ for raters making a binary assessment (eg, yes/no or true/false)? Discuss the purpose of Cohen's κ, its range, and the interpretations of key values such as –1, 0, and 1.C. What other measures can be used to measure reliability for binary, categorical, and continuous data? 3Cruz et al quote the oft-cited Landis and Koch2Landis J.R. Koch G.C. The measurement of observer agreement for categorical data.Biometrics. 1977; 33: 159-174Crossref PubMed Scopus (49675) Google Scholar article stating that a κ of “less than 0.2 represents poor agreement; 0.21 to 0.40, fair agreement; 0.41 to 0.60, moderate agreement; 0.61 to 0.80, good agreement; and 0.81 to 1.00, excellent agreement.” Consider studies of the agreement of airline pilots deciding whether it is safe to land and psychologists deciding whether interviewees have type A or type B personalities. the studies the κ the by Landis and Koch be 2 are in of a and to such as is a a or by a in the for and in the for are and the are to a for each that they percentage agreement is and κ is of are and are that the is the for a the the this the percentage agreement and κ for the the of the are and of the are by the of the are and of the are by the the are and of the are by the and of the are and of the are by the Discuss the of percentage agreement and κ in these Consider the 2 and percentage agreement and κ for is κ the What this that the table the described and that that to 2 in the raters are that are and the raters are that be with with or in with each of κ the in these 2 the of κ, that such that and or are for the and percentage agreement and κ for these is the measure for Consider the of the raters in the in this be reliability is might this be the percentage agreement κ for the in of et The are to indicate the in the and 2 Open table in a new tab A. in the table are with the the pain it to the it to the it to the for these Can you explain why these have percentage agreement you is the the Can you the between the of the in the table and the to κ percentage the problems with percentage agreement and κ in these you think it be the in the of each table of reporting the percentage agreement or et al contains 2 parts, a comparison of the values gathered by trained research assistants and physicians historical information in chest pain and the comparison of these participants' recordings with a “correct” value for each For each part, indicate whether the authors are studying reliability or validity and explain the difference between these part is assessment of and the is assessment of The between reliability and validity is the that the in a that a a The reliability of a to the agreement the the or assessment of validity a observer a or the criterion standard is to be validity studies report the of the observer statistics such as and or reliability such as percentage agreement or What did the authors use as their criterion standard for the validity the and the research it is that their is they a research the of the 2 is What are potential problems with their method of defining the standard? 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What is the range of possible values for percentage 2 and 2 crude percentage agreement for this table is agreement can range between and Calculate Cohen's κ for this table. What is the formula for κ for raters making a binary assessment (eg, yes/no or true/false)? 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the table. the of the and with the of the and for each and and and and each these 2 κ these values to percentage agreement to of reliability is that the reliability data in the agreement is to it is is in that it for agreement that by think of and κ a and are and the to use the values to that each and research these of the and they information about the or of chest pain that might their the of κ are and that the it to the than pain the agreement A B Open table in a new tab The in these to a the table agreement for these the data a of the agreement with for or raters to a that by to that agreement of agreement for the to with are with part of that be to assessment of and raters their in and to their in a is criterion standard to the validity of be that of the in this did in their of of these the of be a to defining and for the of agreement than Can you the between the of the in the table and the to κ percentage that κ is to a to percentage agreement percentage agreement is and is with a 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Meshberg E.G. Shofer F.S. et al.Interrater reliability and accuracy of clinicians and trained research assistants performing prospective data collection in emergency department patients with potential acute coronary syndrome.Ann Emerg Med. 2009; 54: 1-7Abstract Full Text Full Text PDF PubMed Scopus (13) Google Scholar contains 2 parts, a comparison of the values gathered by trained research assistants and physicians about historical information in chest pain patients and the comparison of these participants' recordings with a “correct” value for each item.A. For each part, indicate whether the authors are studying reliability or validity and explain the difference between these concepts.B. What did the authors use as their criterion standard for the validity analysis?C. What are potential problems with their method of defining the criterion (gold) standard? Can you think of alternative approaches?D. The authors report crude agreement and interquartile range for their validity analysis. What part of a distribution is described by the interquartile range? List other statistics used to describe the validity of a measure and why they might be preferable to reporting crude agreement.2Tabled 1MD Recorded “Yes”MD Recorded “No”TotalRA recorded yes1176123RA recorded no18220Total1358143MD, Medical doctor; RA, research assistant. Open table in a new tab A. Calculate the crude percentage agreement for this table. What is the range of possible values for percentage agreement?B. Calculate Cohen's κ for this table. What is the formula for κ for raters making a binary assessment (eg, yes/no or true/false)? Discuss the purpose of Cohen's κ, its range, and the interpretations of key values such as –1, 0, and 1.C. What other measures can be used to measure reliability for binary, categorical, and continuous data? 3Cruz et al quote the oft-cited Landis and Koch2Landis J.R. Koch G.C. The measurement of observer agreement for categorical data.Biometrics. 1977; 33: 159-174Crossref PubMed Scopus (49675) Google Scholar article stating that a κ of “less than 0.2 represents poor agreement; 0.21 to 0.40, fair agreement; 0.41 to 0.60, moderate agreement; 0.61 to 0.80, good agreement; and 0.81 to 1.00, excellent agreement.” Consider studies of the agreement of airline pilots deciding whether it is safe to land and psychologists deciding whether interviewees have type A or type B personalities. the studies the κ the by Landis and Koch be 2 are in of a and to such as is a a or by a in the for and in the for are and the are to a for each that they percentage agreement is and κ is of are and are that the is the for a the the this the percentage agreement and κ for the the of the are and of the are by the of the are and of the are by the the are and of the are by the and of the are and of the are by the Discuss the of percentage agreement and κ in these Consider the 2 and percentage agreement and κ for is κ the What this that the table the described and that that to 2 in the raters are that are and the raters are that be with with or in with each of κ the in these 2 the of κ, that such that and or are for the and percentage agreement and κ for these is the measure for Consider the of the raters in the in this be reliability is might this be the percentage agreement κ for the in of et The are to indicate the in the and 2 Open table in a new tab A. in the table are with the the pain it to the it to the it to the for these Can you explain why these have percentage agreement you is the the Can you the between the of the in the table and the to κ percentage the problems with percentage agreement and κ in these you think it be the in the of each table of reporting the percentage agreement or et al1Cruz C.O. Meshberg E.G. Shofer F.S. et al.Interrater reliability and accuracy of clinicians and trained research assistants performing prospective data collection in emergency department patients with potential acute coronary syndrome.Ann Emerg Med. 2009; 54: 1-7Abstract Full Text Full Text PDF PubMed Scopus (13) Google Scholar contains 2 parts, a comparison of the values gathered by trained research assistants and physicians about historical information in chest pain patients and the comparison of these participants' recordings with a “correct” value for each item.A. For each part, indicate whether the authors are studying reliability or validity and explain the difference between these concepts.B. What did the authors use as their criterion standard for the validity analysis?C. What are potential problems with their method of defining the criterion (gold) standard? Can you think of alternative approaches?D. The authors report crude agreement and interquartile range for their validity analysis. What part of a distribution is described by the interquartile range? List other statistics used to describe the validity of a measure and why they might be preferable to reporting crude agreement.2Tabled 1MD Recorded “Yes”MD Recorded “No”TotalRA recorded yes1176123RA recorded no18220Total1358143MD, Medical doctor; RA, research assistant. Open table in a new tab A. Calculate the crude percentage agreement for this table. What is the range of possible values for percentage agreement?B. Calculate Cohen's κ for this table. What is the formula for κ for raters making a binary assessment (eg, yes/no or true/false)? Discuss the purpose of Cohen's κ, its range, and the interpretations of key values such as –1, 0, and 1.C. What other measures can be used to measure reliability for binary, categorical, and continuous data? 3Cruz et al quote the oft-cited Landis and Koch2Landis J.R. Koch G.C. The measurement of observer agreement for categorical data.Biometrics. 1977; 33: 159-174Crossref PubMed Scopus (49675) Google Scholar article stating that a κ of “less than 0.2 represents poor agreement; 0.21 to 0.40, fair agreement; 0.41 to 0.60, moderate agreement; 0.61 to 0.80, good agreement; and 0.81 to 1.00, excellent agreement.” Consider studies of the agreement of airline pilots deciding whether it is safe to land and psychologists deciding whether interviewees have type A or type B personalities. the studies the κ the by Landis and Koch be 2 are in of a and to such as is a a or by a in the for and in the for are and the are to a for each that they percentage agreement is and κ is of are and are that the is the for a the the this the percentage agreement and κ for the the of the are and of the are by the of the are and of the are by the the are and of the are by the and of the are and of the are by the Discuss the of percentage agreement and κ in these Consider the 2 and percentage agreement and κ for is κ the What this that the table the described and that that to 2 in the raters are that are and the raters are that be with with or in with each of κ the in these 2 the of κ, that such that and or are for the and Calculate percentage agreement and κ for these is the measure for Consider the of the raters in the in this be reliability is might this be the percentage agreement κ for the in of et The are to indicate the in the and 2 Open table in a new tab A. in the table are with the the pain it to the it to the it to the for these Can you explain why these have percentage agreement you is the the Can you the between the of the in the table and the to κ percentage the problems with percentage agreement and κ in these you think it be the in the of each table of reporting the percentage agreement or et al contains 2 parts, a comparison of the values gathered by trained research assistants and physicians historical information in chest pain and the comparison of these participants' recordings with a “correct” value for each For each part, indicate whether the authors are studying reliability or validity and explain the difference between these part is assessment of and the is assessment of The between reliability and validity is the that the in a that a a The reliability of a to the agreement the the or assessment of validity a observer a or the criterion standard is to be validity studies report the of the observer statistics such as and or reliability such as percentage agreement or What did the authors use as their criterion standard for the validity the and the research it is that their is they a research the of the 2 is What are potential problems with their method of defining the standard? 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