In such cases, the most important thing is whether improvement in outcome is worth the higher cost. When conflict of interest exists, validity of RCT should be in question, independent of the behavior of the investigator. Conflict of interest can happen with sponsors like pharmaceutical companies, contract research organization, or at multiple levels. Nowadays, most of the trials are blinded, so, it is exceedingly difficult for investigator to manipulate the data and thus the result.
But it is possible to alter data unintentionally or knowingly at the level of data analysis by data management team. It is important to check at this level, as most investigators would not even know if results were altered by data analyst.
In simple way, conflict of interest can be divided into non-financial type and financial type. Other classifications are negative conflict of interest and positive conflict of interest. More common is that we concern about positive conflict of interest, but negative conflict of interest is also worth observing.
Is bias present in randomized control trial? Bias is defined as systematic error in the results of individual studies or their synthesis. It is worth noticing that financial conflict of interest is not part of this but, it can be motive behind it. Is randomized control trial peer reviewed or not? Another important thing about article publication and reliability is whether peer review done or not.
Peer-review is the assessment of article by qualified people before publication. Peer-review helps to improve the quality of article by adding suggestion, and second it rejects the unacceptable poor-quality articles. Most of the reputed journals made their own policy about peer-review. Peer-review is not free of bias. Sometimes, quality of this process depends on selected qualified faculty and their preference on article.
In nutshell, critical analysis of RCT is all about balancing the strong and weak points of trial based on analyzing main domains such as right question, right population, right study design, right data, and right interpretation.
It is also important to note that these demarcations are immensely simplified, and they are interconnected by many paths. National Center for Biotechnology Information , U. Indian J Crit Care Med. Author information Copyright and License information Disclaimer. A bstract In the era of evidence-based medicine, healthcare professionals are bombarded with plenty of trials and articles of which randomized control trial is considered as the epitome of all in terms of level of evidence.
Keywords: Critical analysis, Evidence based medicine, Randomized control trial. Open in a separate window. Flowchart 1. Table 1 Factors help to formulate sound question 1 , 6. Right Study Design Experimental design considers better over observational design, as they have better grip on variables, and cause—effect hypothesis can be established. Compare data 2. Number of samples 3. Degree of association between variables Parametric method Non-parametric Pearson correlation Spearman rank correlation coefficient Coefficient D.
Table 4 Common effect size indices 26 — For continuous data. Uses mean value and standard deviation of both groups. Odds ratio OR Ratio of 2 odds Small 1. NNT can be used for binary outcome. Does not consider magnitude of baseline mortality rate It should be interpreted with its comparison arm and depending on context. C onclusion In nutshell, critical analysis of RCT is all about balancing the strong and weak points of trial based on analyzing main domains such as right question, right population, right study design, right data, and right interpretation.
Footnotes Source of support: Nil Conflict of interest: None. R eferences 1. Aslam S, Emmanuel P. Formulating a researchable question: a critical step for facilitating good clinical research.
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Sample size calculation. Int J Ayurveda Res. An introduction to power and sample size estimation. Selection of control, randomization, blinding, and allocation concealment. Selection of appropriate statistical methods for research results processing. Int Electron J Math Educ. Selection of appropriate statistical methods for data analysis. Subgroup analyses in confirmatory clinical trials: time to be specific about their purposes. Post hoc analyses: after the facts. Transplantation, Lippincott Williams and Wilkins.
Three simple rules to ensure reasonably credible subgroup analyses. Goodman S. A dirty dozen: twelve P-value misconceptions. Semin Hematol. Kim J, Bang H. Dental Hypotheses, Vol.
Medknow Publications; Three common misuses of P values [internet]. Dahiru T. P-value, a true test of statistical significance? Ann Ibadan Postgrad Med. Jarosz AF, Wiley J.
What are the odds? A practical guide to computing and reporting bayes factors. Available from: [ Google Scholar ]. The 11 study design criteria for this quality assessment, scored as present 1 or absent 0 , were determined to be the most common sources of differential systematic and nondifferential random error in the study designs for TMJD RCTs. Since each study was evaluated only on the published report, it is possible that the specific criteria may have been scored as having not been met but not reported.
Furthermore, the problem of publication bias has not been addressed in this study. Publication bias arises from the tendency for researchers and editors to publish experimental results that are positive while results that are negative or inconclusive are left out or unpublished. This contributes to the overwhelming percent of published articles that demonstrate positive outcomes and thus, systematic reviews may not allow a true indication of the efficacy of a specific treatment.
Regardless, quality reviews can still be useful to help investigators design and publish RCTs with biasing factors considered. The results of this study suggest that many of the universally accepted criteria for clinical trials are often not applied in RCTs of TMJD. Since , the quality of RCTs in TMJD, or the reporting of such, has improved significantly, thus lending more validity to more recent studies Fig 2.
Such inadequacies would predictably have contributed to bias in the study designs, thereby resulting in the heterogeneity in the observed results. Of the four essential Level I criteria, the most common problem was criterion 8 through lack of a defined and concealed randomization process to minimize selection bias. Concealment implies that both the investigator and the subject are blind to and unable to influence the treatment assignment and, thus, the treatment results as well.
Since a defined and concealed randomization process is a well-known requirement, some studies may have met this criterion but did not report it. In these studies, it is best to control all variables possible and consider that some subject bias towards better efficacy may be present.
These groups should be comparable with regard to clinician contact, medication use, and time of follow-up. It is difficult for the reader to know these details unless they are specifically reported. Ninety-three percent of studies attempted to minimize comparison group bias by controlling for baseline differences in prognostic factors.
As noted earlier, randomization cannot guarantee the absence of chance-related baseline imbalances between treatment groups that influence results, especially with sample sizes of 40 or less. It is important to measure at baseline whether groups are comparable with regard to known prognostic factors, such as gender, duration of pain, and depression, and to take between-group differences into account for the analysis.
Such protocol deviations or subjects that are lost to follow-up may produce a distortion of the estimated treatment effects. An intent-to-treat analysis needs to include all subjects randomized independent of any protocol violation so that the inherent statistical assumptions based on the randomized treatment allocation are valid.
Many of the other quality criteria were also not met by most studies. This may be a contributing factor to Type II error false negative in studies that would have shown an effect if an adequate sample size had been used.
The impression may be that this error did not have a biasing effect and cannot be considered a problem in those studies, but this assumption is untrue. Studies with a small sample size are much more likely to have low power suffering from inflated Type II error, finding no difference when one does exist but the opposite can also be true.
However, without taking into account the typical variation in the study factor, it is difficult to know whether a small sample size can accurately represent the target population. Patient compliance with treatment, particularly when the patient plays a role in the active effects of the treatment such as using a splint or performing an exercise, also contributes to significant variability of results. In reviewing criteria 6, few studies considered the ceiling or floor effect in selecting subjects whose baseline symptoms were sufficiently severe enough to detect an active effect of treatment.
Parallel to this matter of symptom severity are the temporal characteristics such as frequency and duration of the signs or symptoms and the need for clinically relevant outcome measures. These temporal clinical characteristics may change sooner and become more clinically relevant than pain intensity with some interventions for TMJD. Without these measurements, important changes in symptoms may remain undetected, resulting again in Type II error.
Quality scores can be used in systematic reviews in a variety of ways including weighing higher-quality studies, applying scores as a threshold for inclusion of a study in a review, as well as with an analysis and comparison of results with other reviews. For example, although weighted composite scores were not used in this review, a good example of the composite scoring approach is presented by Antczak and colleagues. Their proposed quality score included three separate sections: 1 basic identification of the paper for classification purposes, 2 quality of the study protocol, and 3 data analysis and presentation of the paper.
Splints and occlusal adjustments were the two types of occlusal treatments that they examined. These authors determined that the overall quality of these RCT studies was fairly low and the results were equivocal. Although Antczak and colleagues held that meta-analysis was justifiable as the next step after their narrative synthesis of the periodontal treatment evidence, Forssell and Kalso did not, due to the heterogeneity of the TMJD studies that they reviewed.
When the present results are compared to those of Forssell and Kalso, 1 scoring agreement showed a mean ICC of 0. Although the present study included more well-defined criteria, many of the weaknesses of the RCTs found by Forssell and Kalso were also consistent with those identified in the present study.
For example, few studies had appropriate randomization, many did not have blinded measurement of outcome, few measured adherence to treatment, and some did not consider the issues of sample size requirements, attention to dropouts, or the use of co-interventions not defined for the study protocol. This difference between review results may be due to the Forssell and Kalso review being limited to occlusal treatments, whereas the present results were based on a review of six types of treatments and RCTs.
Another design concern found by both reviews was the lack of a run-in period relative to prior treatments, self-care, and medications, with few studies satisfying this quality criterion. Any extraneous treatment such as analgesic medications not defined as part of the experimental or control interventions may influence outcomes and confound the treatment effects.
They need to be matched between groups, eliminated before the study begins during the run-in period, or measured and controlled for in the statistical analysis. There are several limitations to this quality review study.
However, as noted above, the use of the criteria of Antczak et al 22 to compare the present findings with those of Forssell and Kalso 1 showed good agreement between both studies. Second, the searches used in the present study identified RCTs published in the English language but excluded studies in other languages. Thus, while this study attempted to capture the majority of the published literature, it missed some literature that would have had relevance to this review.
Thus, their contribution relative to clinical treatment guidelines and recommendations is questionable. Studies are needed to test TMJD interventions both against placebo groups and other treatments to determine their true relative efficacy. Funding agencies need to insist on standardized methodologies in the review process and ensure that funds are sufficient to conduct high-quality studies.
Emerging information systems involving national registries may be appropriate for standardizing design and data collection for multicenter RCTs. More emphasis should be made on multicenter studies to ensure adequate sample sizes and broad generalizability of the results. Inclusion of the subject flow diagram will provide a description of the progress of participants throughout the study, from the number of potentially eligible individuals for inclusion in the trial, to the number of trial participants in each treatment group who complete the trial.
Editors of journals need to require quality standards in their review processes. This not only encourages investigators to report their methods clearly, but also helps reviewers to assess bias in the study designs accurately. If appropriate design criteria are not met, the investigators should be prepared to justify why they were not applied. Many measures have been already developed and are being used across studies. More research needs to be conducted on effective tools to improve quality and ease of conducting RCTs.
An attempt to standardize measures in chronic pain clinical trials has been initiated by the Initiative on Methods, Measurement, and Pain Assessment in Clinical Trials IMMPACT , which is a collaboration between pain researchers and industry and government agencies. Since it is possible that the specific subtype of TMJD, duration of pain, and comorbid conditions such as fibromyalgia and migraine may be important in determining outcomes of a particular intervention, it is recommended that future studies of TMJD should control for the specific diagnostic subtypes, the duration of pain, and comorbid conditions in the study sample.
Many of the reviewed studies failed to address these issues. Antczak and colleagues have emphasized this issue under Item 2. Pain is the major outcome variable in most TMJD studies but is often susceptible to bias because it is dependent on subject self-report. However, even some examination items may not be completely objective since a patient must endorse pain in response to measures such as palpation pressure.
A concurrent multidimensional data collection is another means for supporting the validity of a self-report. These may be standardized measures for the same construct to establish concurrent validity, or the assessment of other factors that can explain the perception of pain such as emotional factors, subject disposition, and global improvement.
It is expected that future RCTs in TMJD will be improved due to a growing awareness of the essential study design criteria and study reporting requirements. This is also supported by the trend towards such improvement occurring over time, as illustrated in Fig 2. The view of the authors is that quantitative estimates of benefit should be performed using emerging meta-analysis procedures and pooling the results of RCTs with similar interventions and comparison groups.
The relative contribution of each study can be weighted by its respective standard error and its heterogeneity relative to the overall body of evidence. Thus, it is reasonable to explore existing quantitative evidence using current mathematical methods to obtain information that can then be compared to the qualitative narrative syntheses.
In certain areas of medicine, observational studies and nonrandomized controlled studies have an important application such as cohort studies comparing effectiveness, outcome quantification, and risk factor identification. However, the RCT is the study design recommended to assess the effectiveness of specific interventions and should be the design of choice to avoid susceptibility to systematic bias.
But there has been a trend toward improvement in study quality over time. A hierarchy of steps is proposed for clinicians to evaluate critically the internal and external validity of studies of interest. It is hoped that by discussing these methods used in past RCTs, important improvements and standardization will be stimulated for future RCTs. Ultimately, improvement in RCT methods will allow better understanding and comparison of studies.
The combining of their results by meta-analysis will also maximize the benefits obtained from clinical trial research. Notwithstanding the difficulty of many studies to meet essential criteria, and to minimize systematic bias, the available evidence needs to be fully analyzed using existing as well as newly emerging mathematical methods to synthesize the results.
This will ultimately improve clinical guidelines and the care of TMJD patients. James R. Donald R. Nixdorf, University of Minnesota, Minneapolis, Minnesota. Eric L. John O. National Center for Biotechnology Information , U. J Orofac Pain. Author manuscript; available in PMC Aug Author information Copyright and License information Disclaimer.
Copyright notice. See other articles in PMC that cite the published article. Abstract Aims To evaluate the quality of methods used in randomized controlled trials RCTs of treatments for management of pain and dysfunction associated with temporomandibular muscle and joint disorders TMJD and to discuss the implications for future RCTs.
Methods A systematic review was made of RCTs that were implemented from through March , to evaluate six types of treatments for TMJD: orthopedic appliances, occlusal therapy, physical medicine modalities, pharmacologic therapy, cognitive-behavioral and psychological therapy, and temporomandibular joint surgery.
Results Independent assessments by raters demonstrated consistency with a mean intraclass correlation coefficient of 0. Conclusions Much of the evidence base for TMJD treatments may be susceptible to systematic bias and most past studies should be interpreted with caution.
The appropriateness of data analysis and presentation. The ethical implications of the intervention being evaluated. They suggested the following questions for critical appraisal of an RCT quality: Did the trial address a clearly focused issue?
This is similar to how clinical practice guidelines consider the entire evidence base and the nature of the interventions being compared including costs, burden of implementation and patient preferences [ 1 ]. Thus, a nuanced set of standardised policy responses to more nuanced evidence summaries may be warranted to ensure some standardisation of interpretation and implementation, while still considering differences in patient characteristics and preferences. The primary RCT results generally represent the average treatment effects across all included patients, however, heterogeneity of treatment effects HTE [ 69 , 70 ] in subpopulations are likely, and, despite being difficult to prove, have been suggested in multiple previous critical care RCTs [ 33 , 64 , 71 , 72 , 73 , 74 ].
A neutral average effect may represent benefit in some patients and harm in others Fig. It is sometimes assumed that the risk of adverse events is similar for patients at different risk of the primary outcome [ 70 ], which may affect the balance between benefits and harms of a treatment according to baseline risk, although this assumption may not always hold [ 77 ].
Heterogeneity of treatment effects in clinical trial. Forest plot illustrating a fictive clinical trial enrolling patients. In this trial, the average treatment effect may be considered neutral with a relative risk RR of 0. The trial population consists of three fictive subgroups with heterogeneity of treatment effects: A, with an intervention effect that is neutral or inconclusive , similarly to the pooled result; B, with substantial benefit from the intervention; and C, with substantial harm from the intervention.
If only the average intervention effect is assessed, it may be concluded — based on the apparent neutral overall result — that whether the intervention or control is used has little influence on patient outcomes, and it may be missed that the intervention provides substantial benefit in some patients and substantial harm in others.
Similarly, an intervention with an overall beneficial effect may be more beneficial in some subgroups than others and may provide harm in some patients, and vice versa.
While large, pragmatic RCTs may be preferred for detecting clinically relevant average treatment effects, guiding overall clinical practice recommendations and for public healthcare, they have been criticised for including too heterogenous populations, often due to inclusion of general acutely ill ICU patients or ICU patients with broad syndromic conditions, i.
Even if present, HTE may be of limited importance if some patients benefit while others are mostly unaffected, if cost or burden of implementation is limited, or if some patients are harmed while others are mostly unaffected.
As substantially more patients are required to assess subgroup differences than for primary analyses, most subgroup analyses are substantially underpowered and may miss clinically relevant differences [ 79 ].
In addition, larger numbers of subgroup analyses increase the risk of chance findings [ 79 ]. Conventional subgroup analyses assess one characteristic at a time, which may not reflect biology or clinical practice where multiple risk factors are often synergistic or additive [ 79 ], or where effect modifiers may be dynamic and change during illness course. Finally, conventional subgroup analyses frequently dichotomise continuous variables, which limits power [ 80 ] and makes assessment of gradual changes in responses difficult.
Regardless of the approach, appropriate caution should always be employed when interpreting subgroup and HTE analyses. Adaptive trials are more flexible and can be more efficient than conventional RCTs [ 85 ], while being designed to have similar error rates. Adaptive trials often, but not always, use Bayesian statistical methods, which are well suited for continuous assessment of accumulating evidence [ 83 , 86 ].
Adaptive trials can be adaptive in multiple ways [ 87 ]. Expected sample sizes are estimated using simulation; if the expected baseline risks and effect sizes are incorrect, the final sample sizes will differ from expectations, but adaptive trials are still able to continue until sufficient evidence is obtained. Further, adaptive sample sizes are better suited for new diseases, where no or limited existing knowledge complicates sample size calculations.
Second, trials may be adaptive regarding the interventions assessed; multiple interventions or doses may be studied simultaneously or in succession, and the least promising may be dropped while assessment of better performing interventions continues until conclusive evidence has been obtained [ 83 , 86 ].
This has been used for dose-finding trials, e. Similarly, interventions may be added during the trial, as in platform trials discussed below. Third, trials may use response-adaptive randomisation to update allocation ratios based on accumulating evidence, thereby increasing the chance that patients will be allocated to more promising interventions, despite not having reached conclusiveness yet.
This can increase efficiency in some situations, but also decrease it, as in two-armed RCT and some multi-armed RCTs [ 90 , 91 ]. Thus, it has been argued that while response-adaptive randomisation may benefit internal patients, it may not always be preferable, as it can lead to slower discovery of interventions that can benefit patients external to the trial in some cases [ 91 , 92 ].
Platform trials are RCTs that instead of focussing on single intervention comparisons focus on a disease or condition and assess multiple interventions according to a master protocol [ 83 , 93 ].
Platform trials may run perpetually, with interventions added or dropped continuously [ 83 , 94 ] and often employ multiple adaptive features and probabilistic decision rules [ 83 , 93 ]. Interventions assessed can be nested in multiple domains, e. By assessing multiple interventions simultaneously and by re-using controls for comparisons with multiple interventions, platform trials can be more efficient than sequential two-armed comparisons and can be more efficient than simpler adaptive trials [ 94 , 95 ].
If response-adaptive randomisation is used, probabilities of allocation to potentially superior interventions increases as evidence is accumulated, and interventions that are deemed superior may immediately become implemented as standard of care by becoming the new control group [ 83 ].
Thus, implementation of results into practice — at least in participating centres—may become substantially faster. Comparable to how data from multiple conventional RCTs may be prospectively planned to be analysed together, data from multiple platform trials may be combined in multiplatform trials with similar benefits and challenges as individual platform trials and standardisation across individual, conventional RCTs [ ].
In addition to the possible tighter integration between research and clinical practice that may come with adaptive platform trials and ultimately may lead to learning healthcare systems [ 83 ], integration may be increased in other ways. Trials may be embedded in electronic health records, where automatic integration may lead to substantial logistic improvements regarding data collection, integration of randomisation modules, and alerts about potentially eligible patients.
This may improve logistics and data collection and facilitate closer integration between research and practice [ 61 , 83 ]. Similarly, RCTs may use data already collected in registers or clinical databases, substantially decreasing the data-collection burden, as has been done in, e.
Finally, fostering an environment where clinical practice and clinical research are tightly integrated and where enrolment in clinical trials is considered an integral part of clinical practice in individual centres by clinicians, patients and relatives may lead to faster improvements of care for all patients.
While the methods discussed may mitigate some challenges of conventional RCTs, they are not without limitations Table 1. First, larger trials come with challenges regarding logistics, regulatory requirements including approvals, consent procedures, and requirements for reporting adverse events , economy, collaboration, between-centre heterogeneity in other interventions administered, and potential challenges related to academic merits.
Second, standardisation and meta-analyses may require compromises or increased data-collection burden in some centres or may not be possible due to between-trial differences.
Third, while complete research programmes may lead to better RCTs, they may not be possible in, e. Fourth, using outcomes other than mortality comes with difficulties relating to statistical analysis, how death is handled and possibly interpretation, and mortality should not be abandoned for outcomes that are not important to patients.
Fifth, while avoiding dichotomisation of results and using Bayesian methods has some advantages, it may lead to larger differences in how evidence is interpreted and possibly lower thresholds for accepting new evidence if adequate caution is not employed. In addition, switching to Bayesian methods requires additional education of clinicians, researchers and statisticians, and specification of priors and estimating required sample sizes adds complexity.
Sixth, while improved analyses of HTE have benefits compared to conventional subgroup analyses, the risk of chance findings and lack of power remains.
Finally, adaptive and platform trials come with logistic and practical challenges as listed in Table 1 and discussed below. As adaptive and platform trials are substantially less common than more conventional RCTs, there is less methodological guidance and interpretation may be more difficult for readers.
Fortunately, several successful platform trials have received substantial coverage in the critical care community [ 64 , 99 ], and an extension for the Consolidated Standards of Reporting Trials CONSORT statement for adaptive trials was recently published [ ]. Planning adaptive and platform trials comes with additional logistic and financial challenges related to the current project-based funding model, which is better suited for fixed-size RCTs [ 83 , 85 , 93 ].
While adaptive trials are more flexible, large samples may still be required to firmly assess all clinically relevant effect sizes, which may not always be feasible. In addition, statistical simulation is required instead of simple sample size estimations [ 83 , 94 ]. Further, the regulatory framework for adaptive and platform trials is less well-developed than for conventional RCTs, and regulatory approvals may thus be more complex and time-consuming [ 83 ].
There are also challenges with the adaptive features, and careful planning is necessary to avoid aggressive adaptations to random, early fluctuations. Simulation may be required to ensure that the risk of stopping due to chance is kept at an acceptable level, analogous to alpha-spending functions in conventional, frequentist trials [ ]. Finally, comparisons with non-concurrent controls may affect interpretation and introduce bias if inappropriately handled [ ].
Adaptations require continues protocol amendments and additional resources to implement and communicate, and may require additional training when new interventions are added [ ]. We expect that the discussed methodological features will become more common in future critical care RCTs, and that this will improve efficiency and flexibility, and may help answer more complex questions. These methods come with challenges, though, and conventional RCTs may be preferred for simple, straightforward comparisons.
Some challenges may be mitigated as these designs become more familiar to clinicians and researchers, and as additional methodological guidance is developed. We expect the future critical care RCT landscape to be a mix of relatively conventional RCTs and more advanced, adaptive trials. We propose that researchers consider the optimal methodological approach carefully when planning new RCTs. While different designs may be preferable in different situations, the choice should be based on careful thought instead of convenience or tradition, and more advanced approaches may be necessary in some situations to move critical care RCTs and practice forward.
In this review, we have discussed challenges and limitations of conventional RCTs, along with recent developments, novel methodological approaches and their advantages and potential disadvantages. We expect critical care RCTs to evolve and improve in the coming years. At its core, however, the most central feature of any RCT remains the randomisation itself, which provides unparalleled protection against confounding.
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