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Charles E; Crook L eds. Expose: The failure of family courts to protect children from abuse in custody disputes. D, Marc J. Clinician's Guide to Child Custody Evaluations. John Wiley and Sons. Journal of Child Custody. In Gardner, Richard A. Richard; Lorandos, Demosthenes eds.

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Charles C. Queen's Law Journal. Archived from the original on Encyclopedia of Interpersonal Violence. In O'Brien J ed. Encyclopedia of Gender and Society. Oxford University Press. American Psychological Association. Children's Rights and the Developing Law. Cambridge University Press. Children: The Modern Law. Men's News Daily. Pittsburgh Post-Gazette. Retrieved 2 March American Psychiatric Association. Archived from the original on 5 October Huffington Post. Psych Central. Retrieved 4 May Journal of Child Custody: 37— New York: The Guilford Press. Journal of the American Academy of Psychiatry and the Law.

Brianna; Alvis, Lindsey J. Not According to Scientific Evidence. Journal of Child Sexual Abuse. Clinician's guide to child custody evaluations. American Prosecutors Research Institute Newsletter. American Journal of Family Law. Department of Justice. Family Law. Myers on evidence in child, domestic, and elder abuse cases.

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Gaithersburg, Md: Aspen Publishers. L 'analyse de contenu Content analysis. Paris, France: PUF. Bargai, N. Posttraumatic stress disorder and depression in battered women: The mediating role of learned helplessness. Journal of Family Violence, 22, Blake, D. Co-occurrence and correlates of posttraumatic stress disorder and major depression in physically abused women. Journal of Family Violence, 14, Colwell, K.

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Applied Cognitive Psychology, 19, Psicothema, 7, Fisher, R. Memory-enhancing techniques for investigative interview. Sprinfield, IL: Charles C. Foa, E. Reliability and validity of a brief instrument for assessing posttraumatic stress disorder. Journal of Traumatic Stress, 6, Graham, J. MMPI Assessing personality and psychopathology 4th ed. Greene, R. Malingering and defensiveness on the MMPI Rogers Ed. Hathaway, S. The Minnesota Multiphasic Personality Inventory Keane, T. Empirical development of an MMPI subscale for the assessment of combat-related posttraumatic stress disorder. Journal of Consulting and Clinical Psychology, 52, Kessler, R.

Posttraumatic stress disorder in the national comorbidity survey. Archives of General Psychiatry, 52, The cognitive interview: A meta-analysis. Konecni, V. Methodological issues on legal decision-making, with special reference to experimental simulations. Bliesener Eds. International perspectives pp. Berlin, Germany: Walter de Gruyter. Memon, A. Cognitive interview: A meta-analytic review and study space analysis of the past 25 years. Psychology, Public Policy, and Law, 16, O'Donnell, M.

Bryant, R. Posttraumatic disorders following injury: Assessment and other methodological considerations. Young, A. Nicholson Eds. New York, NY: Springer. Pico-Alfonso, M. Psychological intimate partner violence: The major predictor of posttraumatic stress disorder in abused women. Neuroscience and BiobehavioralReviews, 29, Polusny, M. Assessment of psychological distress and disability after sexual assault in adults. Pope, K. A practical guide for expert witnesses and attorneys. Resnick, P.

Malingering of posttraumatic disorders. Rogers, R. Current status of clinical methods. Researching response styles. Sewell, K. Assessment, 10, Rosenfeld, B. What to do with contradictory data? Approaches to the integration of multiple malingering measures. International Journal of Forensic Mental Health, 9, Sarasua, B. Psychopathological profile of battered women according to age. Psicothema, 19, Spitzer, R. Washington, D. Steller, M. Child sexual abuse: Forensic interviews and assessment. United Nations.

Committee on crime prevention and control. Report on the tenth session. Vienna, Switzerland: Author. Discriminating real victims from feigners of psychological injury in gender violence: Validating a protocol for forensic settings. When the target audiences for a guideline are clinicians and the patients they treat, the perspective would generally be that of the patient.

Not infrequently, outcomes of most importance to patients remain unexplored. When important outcomes are relatively infrequent, or occur over long periods of time, investigators often choose to measure substitutes, or surrogates, for those outcomes. When this is the case, they should specify the population-important outcomes and, if necessary, the surrogates they are using to substitute for those important outcomes.

Guideline developers should not list the surrogates themselves as their measures of outcome. The necessity to substitute the surrogate may ultimately lead to rating down the quality of the evidence because of the indirectness see Chapter Quality of evidence. The endpoint for systematic reviews and for HTA restricted to evidence reports is a summary of the evidence, the quality rating for each outcome and the estimate of effect.

For guideline developers and HTA that provide advice to policymakers, a summary of the evidence represents a key milestone on the path to a recommendation. The evidence collected from systematic reviews is used to produce GRADE evidence profile and summary of findings table. Evidence tables are a method for presenting the quality of the available evidence, the judgments that bear on the quality rating, and the effects of alternative management strategies on the outcomes of interest. Clinicians, patients, the public, guideline developers, and policy-makers require succinct and transparent evidence summaries to support their decisions.

While an unambiguous health care question is key to evidence summaries, the requirements for specific users may differ in content and detail. Therefore, the format of each table may be different depending on user needs. Two approaches with iterations for evidence tables are available, which serve different purposes and are intended for different audiences:. After completing the information to populate the tables, the information will be stored and can be updated accordingly.

Different formats for each aproach, chosen according to what the target audience may prefer, are available. See online tutorials at: cebgrade.

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It is intended for review authors, those preparing SoF tables and anyone who questions a quality assessment. It helps those preparing SoF tables to ensure that the judgments they make are systematic and transparent and it allows others to inspect those judgments. Guideline panels should use evidence profiles to ensure that they agree about the judgments underlying the quality assessments. A GRADE evidence profile allows presentation of key information about all relevant outcomes for a given health care question. A GRADE evidence profile is particularly useful for presentation of evidence supporting a recommendation in clinical practice guidelines but also as summary of evidence for other purposes where users need or want to understand the judgments about the quality of evidence in more detail.

Summary of Findings tables provide a summary of findings for each of the included outcomes and the quality of evidence rating for each outcome in a quick and accessible format, without details of the judgements about the quality of evidence. They are intended for a broader audience, including end users of systematic reviews and guidelines.

They provide a concise summary of the key information that is needed by someone making a decision and, in the context of a guideline, provide a summary of the key information underlying a recommendation. The format of SoF tables produced using the Guideline Development Tool has been refined over the past several years through wide consultation, user testing, and evaluation.

It is designed to support the optimal presentation of the key findings of systematic reviews. The SoF table format has been developed with the aim of ensuring consistency and ease of use across reviews, inclusion of the most important information needed by decision makers, and optimal presentation of this information. However, there may be good reasons for modifying the format of a SoF table for some reviews. Systematic reviews that address more than one main comparison e. It is likely that all studies relevant to a health care question will not provide evidence regarding every outcome.

Indeed, there may be no overlap between studies providing evidence for one outcome and those providing evidence for another. Because most existing systematic reviews do not adequately address all relevant outcomes, the GRADE process may require relying on more than one systematic review. GRADE provides a specific definition of the quality of evidence that is different in the context of making recommendations and in the context of summarizing the findings of a systematic review. As GRADE suggests somewhat different approaches for rating the quality of evidence for systematic reviews and for guidelines, the handbook highlights guidance that is specific to each group.

Guideline panels must make judgments about the quality of evidence relative to the specific context for which they are using the evidence. The GRADE approach involves separate grading of quality of evidence for each patient-important outcome followed by determining an overall quality of evidence across outcomes.

Because systematic reviews do not, or at least should not, make recommendations, they require a different definition. Authors of systematic reviews grade quality of a body of evidence separately for each patient-important outcome. The quality of evidence is rated for each outcome across studies i. This does not mean rating each study as a single unit. Example 1: Quality of evidence may differ from one outcome to another within a single study. In a series of unblinded RCTs measuring both the occurrence of stroke and all-cause mortality, it is possible that stroke - much more vulnerable to biased judgments - will be rated down for risk of bias, whereas all-cause mortality will not.

Similarly, a series of studies in which very few patients are lost to follow-up for the outcome of death, and very many for the outcome of quality of life, is likely to result in judgments of lower quality for the latter outcome. Problems with indirectness may lead to rating down quality for one outcome and not another within a study or studies if, for example, fracture rates are measured using a surrogate e.

We are very confident that the true effect lies close to that of the estimate of the effect. We are moderately confident in the effect estimate: The true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different. Our confidence in the effect estimate is limited: The true effect may be substantially different from the estimate of the effect.

We have very little confidence in the effect estimate: The true effect is likely to be substantially different from the estimate of effect. Quality of evidence is a continuum; any discrete categorisation involves some degree of arbitrariness. Nevertheless, advantages of simplicity, transparency, and vividness outweigh these limitations.

The GRADE approach to rating the quality of evidence begins with the study design trials or observational studies and then addresses five reasons to possibly rate down the quality of evidence and three to possibly rate up the quality. The subsequent sections of the handbook will address each of the factors in detail. Table 5. Limitations in study design or execution risk of bias.

All plausible confounding would reduce the demonstrated effect or increase the effect if no effect was observed. When the body of evidence is intermediate with respect to a particular factor, the decision about whether a study falls above or below the threshold for up- or downgrading the quality by one or more factors depends on judgment. For example, if there was some uncertainty about the three factors: study limitations, inconsistency, and imprecision, but not serious enough to downgrade each of them, one could reasonably make the case for downgrading, or for not doing so.

A reviewer might in each category give the studies the benefit of the doubt and would interpret the evidence as high quality. Another reviewer, deciding to rate down the evidence by one level, would judge the evidence as moderate quality. Reviewers should grade the quality of the evidence by considering both the individual factors in the context of other judgments they made about the quality of evidence for the same outcome. In such a case, you should pick one or two categories of limitations which you would offer as reasons for downgrading and explain your choice in the footnote.

You should also provide a footnote next to the other factor, you decided not to downgrade, explaining that there was some uncertainty, but you already downgraded for the other factor and further lowering the quality of evidence for this outcome would seem inappropriate.

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Despite the limitations of breaking continua into categories, treating each criterion for rating quality up or down as discrete categories enhances transparency. Source of control group results is implicit or unclear, thus, they will usually warrant downgrading from low to very low quality evidence.

Expert opinion represents an interpretation of evidence in the context of experts' experiences and knowledge. Experts may have opinion about evidence that may be based on interpretation of studies ranging from uncontrolled case series e. It is important to describe what type of evidence whether published or unpublished is being used as the basis for interpretation. The following sections discuss in detail the 5 factors that can result in rating down the quality of evidence for specific outcomes and, thereby, reduce confidence in the estimate of the effect.

Limitations in the study design and execution may bias the estimates of the treatment effect. Our confidence in the estimate of the effect and in the following recommendation decreases if studies suffer from major limitations. The more serious the limitations are, the more likely it is that the quality of evidence will be downgraded. Numerous tools exist to evaluate the risk of bias in randomized trials and observational studies. Our confidence in an estimate of effect decreases if studies suffer from major limitations that are likely to result in a biased assessment of the intervention effect.

Patient, caregivers, those recording outcomes, those adjudicating outcomes, or data analysts are aware of the arm to which patients are allocated or the medication currently being received in a crossover trial. Incomplete accounting of patients and outcome events. Loss to follow-up and failure to adhere to the intention-to-treat principle in superiority trials; or in noninferiority trials, loss to follow-up, and failure to conduct both analyses considering only those who adhered to treatment, and all patients for whom outcome data are available.

The significance of particular rates of loss to follow-up, however, varies widely and is dependent on the relation between loss to follow-up and number of events. The higher the proportion lost to follow-up in relation to intervention and control group event rates, and differences between intervention and control groups, the greater the threat of bias.

Incomplete or absent reporting of some outcomes and not others on the basis of the results. Systematic reviews of tools to assess the methodological quality of non-randomized studies have identified over checklists and instruments. Failure to develop and apply appropriate eligibility criteria inclusion of control population. Especially within prospective cohort studies, both groups should be followed for the same amount of time. Depending on the context and study type, there can be additional limitations than those listed above.

Guideline panels and authors of systematic reviews should consider all possible limitations. Guideline panels or authors of systematic reviews should consider the extent to which study limitations may bias the results see Examples 1 to 7. If the limitations are serious they may downgrade the quality rating by one or even two levels. Moving from risk of bias criteria for each individual study to a judgment about rating down for quality of evidence for risk of bias across a group of studies addressing a particular outcome presents challenges.

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We suggest the following principles:. Systematic reviewers working within the context of Cochrane Systematic Reviews, can use the following guidance to assess study limitations risk of bias in Cochrane Reviews. These assessments should feed directly into the assessment of study limitations. Cochrane systematic review authors must use their judgment to decide between alternative categories, depending on the likely magnitude of the potential biases. Every study addressing a particular outcome will differ, to some degree, in the risk of bias. Review authors must make an overall judgment on whether the quality of evidence for an outcome warrants downgrading on the basis of study limitations.

The assessment of study limitations should apply to the studies contributing to the results in the Summary of Findings table, rather than to all studies that could potentially be included in the analysis. Most information is from studies at low risk of bias. Plausible bias unlikely to seriously alter the results. Most information is from studies at low or unclear risk of bias. Plausible bias that raises some doubt about the results. Potential limitations are unlikely to lower confidence in the estimate of effect.

Potential limitations are likely to lower confidence in the estimate of effect. The proportion of information from studies at high risk of bias is sufficient to affect the interpretation of results. Plausible bias that seriously weakens confidence in the results. Crucial limitation for one criterion, or some limitations for multiple criteria, sufficient to lower confidence in the estimate of effect. Crucial limitation for one or more criteria sufficient to substantially lower confidence in the estimate of effect. A systematic review investigated whether fewer people with cancer died when given anti-coagulants compared to a placebo.

There were 5 RCTs. Three studies had unclear sequence generation as it was not reported by authors and one study contributing few patients to the meta-analysis had unclear allocation concealment, and incomplete outcome data. In this case, the overall limitations were not serious and the evidence was not downgraded for risk of bias. A systematic review of the effects of testosterone on erection satisfaction in men with low testosterone identified four RCTs. Data from the three smaller trials suggested a large treatment effect 1. The authors could not obtain the missing data, and could not be confident that the large treatment effect was certain, therefore, they rated down the body of evidence for selective reporting bias in the largest study.

In another scenario, the review authors did obtain the complete data from the larger trial. After including the less impressive results of the large trial, the magnitude of the effect was smaller and no longer statistically significant 0. In that case, the evidence would not be downgraded. RCTs of the effects of Intervention A on acute spinal injury measured both all-cause mortality and, based on a detailed physical examination, motor function.

The outcome assessors were not blinded for any outcomes. Blinding of outcome assessors is less important for the assessment of all-cause mortality, but crucial for motor function. The quality of the evidence for the mortality outcome may not be downgraded. However, the quality may be downgraded for the motor function outcome. A systematic review of 2 RCTs showed that family therapy for children with asthma improved daytime wheeze.

However, allocation was clearly not concealed in the two included trials. This limitation might warrant downgrading the quality of evidence by one level. A review was conducted to assess the effects of early versus late treatment of influenza with oseltamivir in observational studies. Researchers found 8 observational studies which assessed the risk of mortality. The statistical analysis in all 8 studies did not adjust for potential confounding risk factors such as age, chronic lung conditions, vaccination or immune status.

The quality of the evidence was therefore downgraded from low to very low for serious limitations in study design. Three RCTs of the effects of surgery on patients with lumbar disc prolapse measured symptoms after 1 year or longer. The RCTs suffered from inadequate concealment of allocation, and unblinded assessment of outcome by potentially biased raters surgeons using a non-validated rating instrument.

The benefit of surgery is uncertain. The quality of the evidence was downgraded by two levels due to these study limitations quality. These very serious limitations would warrant downgrading the quality of evidence by two levels, from high to low. True differences in the underlying treatment effect may be likely when there are widely differing estimates of the treatment effect i. Investigators should explore explanations for heterogeneity, and if they cannot identify a plausible explanation, the quality of evidence should be downgraded. Whether it is downgraded by one or two levels will depend on the magnitude of the inconsistency in the results.

Patients vary widely in their pre-intervention or baseline risk of the adverse outcomes that health care interventions are designed to prevent e. As a result, risk differences absolute risk reductions in subpopulations tend to vary widely. Relative risk RR reductions, on the other hand, tend to be similar across subgroups, even if subgroups have substantial differences in baseline risk. When easily identifiable patient characteristics confidently permit classifying patients into subpopulations at appreciably different risk, absolute differences in outcome between intervention and control groups will differ substantially between these subpopulations.

This may well warrant differences in recommendations across subpopulations, rather than downgrading the quality evidence for inconsistency in effect size. Although there are statistical methods to measure heterogeneity, there are a variety of other criteria to assess heterogeneity, which can also be used when results cannot be pooled statistically.

Criteria to determine whether to downgrade for inconsistency can be applied when results are from more than one study and include:. It is also important to note the implicit limitations in this statistic. All statistical approaches have limitations, and their results should be seen in the context of a subjective examination of the variability in point estimates and the overlap in CIs.

Example 1: Differences in direction, but minimal heterogeneity. Consider the figure below; a forest plot with four studies, two on either side of the line of no effect. We would have no inclination to rate down for inconsistency. Differences in direction, in and of themselves, do not constitute a criterion for variability in effect if the magnitude of the differences in point estimates is small. Example 2: When inconsistency is large, but differences are between small and large beneficial effects.

Even when inconsistency is large, it may not reduce confidence in results regarding a particular decision. Consider, the figure below in which variability is substantial, but the differences are between small and large treatment effects. Guideline developers may or may not consider this degree of variability important. Systematic review authors, much less in a position to judge whether the apparent high heterogeneity can be dismissed on the grounds that it is unimportant, are more likely to rate down for inconsistency.

Example 3: Substantial heterogeneity, of unequivocal importance. Consider the figure below. The magnitude of the variability in results is identical to that of the figure presented in Example 2. However, because two studies suggest benefit and two suggest harm, we would unquestionably choose to rate down the quality of evidence as a result of inconsistency. Example 4: Test a priori hypotheses about inconsistency even when inconsistency appears to be small. Yet, when the investigators examined the effect in trials that used an external endpoint committee RR 3. Although the issue is controversial, we recommend that meta-analyses include formal tests of whether a priori hypotheses explain inconsistency between important subgroups even if the variability that exists appears to be explained by chance e.

If the effect size differs across studies, explanations for inconsistency may be due to differences in:. Guideline panelists are then likely to offer different recommendations for different patient groups and interventions. If large variability in magnitude of effect remains unexplained and authors fail to attribute it to differences in one of these four variables, then the quality of evidence decreases.

Uncertainty relates to how important inconsistency is to the confidence in the result. The extent is used to decide whether to downgrade the quality rating by one or even two levels. Example 5: Making separate recommendations for subpopulations. When the analysis for benefits of endarterectomy was pooled across patients with stenosis of the carotid artery, there was high heterogeneity. Heterogeneity was explored and was explained by separating out patients who were symptomatic with high degree stenosis in which endarterectomy was beneficial , and patients who were asymptomatic with moderate degree stenosis in which surgery was not beneficial.

The authors presented and graded the evidence by patient group and did not downgrade the quality of the evidence for inconsistency. Two different recommendations were also made according to patient group by the guideline panel. Finding an explanation for inconsistency is preferable. An explanation can be based on differences in population, intervention, or outcomes which mandate two or more estimates of effect, possibly with separate recommendations. However, subgroups effects may prove spurious and may not explain all the variability in the extent of inconsistency.

Indeed, most putative subgroup effects ultimately prove spurious. A cautionary note about subgroup analyses and their presentation is warranted; refer to Sun et al. Review authors and guideline developers must exercise a high degree of skepticism regarding potential subgroup effect explanations, paying particular attention to criteria the following 7 criteria:. Judgement is required to determine how convincing a subgroup analysis is based on the above criteria. Example 6: Subgroup analysis explaining inconsistency in results.

In patients with severe disease labeled acute respiratory distress syndrome , the effect more clearly favored the high PEEP strategy RR 0. Applying the seven criteria see table below , we find that six are met fully, and the seventh, consistency across trials and outcomes, partially: the results of the subgroup analysis were consistent across the three studies, but other ways of measuring severity of lung injury for instance, treating severity as a continuous variable failed to show a statistically significant interaction between the severity and the magnitude of effect.

In this case, the subgroup analysis is relatively convincing. Example 7: Subgroup analysis not very likely to explain inconsistency in results. Three randomized trials have tested the effects of vasopressin vs. The results show appreciable differences in point estimates, widely overlapping CIs, a p-value for the test of heterogeneity of 0. Two of the trials included both patients in whom asystole was responsible for the cardiac arrest and the patients in whom ventricular fibrillation was the offending rhythm.

One of these two trials reported a borderline statistically significant benefit - our own analysis was borderline nonsignificant - of vasopressin over epinephrine restricted to patients with asystole in contrast to patients whose cardiac arrest was induced by ventricular fibrillation.

It is not very likely that the subgroup analysis can explain the moderate inconsistency in the results. Chance can explain the putative subgroup effect and the hypothesis fails other criteria including small number of a priori hypotheses and consistency of effect. Here, guideline developers should make recommendations on the basis of the pooled estimate of data from both the groups.

Whether the quality of evidence should be rated down for inconsistency is another judgment call; we would argue for not rating down for inconsistency. We are more confident in the results when we have direct evidence. Direct evidence consists of research that directly compares the interventions which we are interested in, delivered to the populations in which we are interested, and measures the outcomes important to patients. Authors of systematic reviews and guideline panels making recommendations should consider the extent to which they are uncertain about the applicability of the evidence to their relevant question and downgrade the quality rating by one or even two levels.

Directness is judged by the users of evidence tables, depending on the target population, intervention, and outcomes of interest. Authors of systematic reviews should answer the health care question they asked and, thus, they will rate the directness of evidence they found.

The considerations made by the authors of systematic reviews may be different than those of guideline panels that use the systematic reviews. The more clearly and explicitly the health care question was formulated the easier it will be for the users to understand systematic review authors' judgments. Differences between study populations within a systematic review are a common problem for systematic review authors and guideline panels. When this occurs evidence is indirect. The effect on overall quality of evidence will vary depending on how different the study populations are, as a result quality may not decrease, decrease by a one level or decrease by two levels in extreme cases.

The above discussion refers to different human populations, but sometimes the only evidence will be from animal studies, such as rats or primates. In general, we would rate such evidence down two levels for indirectness. Animal studies may, however, provide an important indication of drug toxicity. Although toxicity data from animals does not reliably predict toxicity in humans, evidence of animal toxicity should engender caution in recommendations. Other types of nonhuman studies e.

High-quality randomized trials have demonstrated the effectiveness of antiviral treatment for seasonal influenza. The panel judged that the biology of seasonal influenza was sufficiently different from that of avian influenza avian influenza organism may be far less responsive to antiviral agents than seasonal influenza that the evidence required rating down quality by two levels, from high to low, due to indirectness. Example 2: Non-human studies providing high quality evidence Not Downgraded.

Consider laboratory evidence of change in resistance patterns of bacteria to antimicrobial agents e. These laboratory findings may constitute high quality evidence for the superiority of antibiotics to which MRSA is sensitive vs. Systematic reviewers will make a concerted effort to ensure that only studies with directly relevant interventions are included in their review. However, exceptions may still occur. Generally, when interventions that are indirectly related to the study are included in systematic review, evidence quality will be decreased.

In some instances the intervention used will be the same, but may be delivered in differently depending on the setting. Example 3: Interventions delivered differently in different settings Downgraded by One Level. A systematic review of music therapies for autism found that trials tested structured approaches that are used more commonly in North America than in Europe. Because the interventions differ, the results from structured approaches are more applicable to North America and the results of less structured approaches are more applicable in Europe.

Guideline panelists should consider rating down the quality of the evidence if the intervention cannot be implemented with the same rigor or technical sophistication in their setting as in the RCTs from which the data come. Guideline developers may often find the best evidence addressing their question in trials of related, but different, interventions. A guideline addressing the value of colonoscopic screening for colon cancer will find the randomized control trials RCTs of fecal occult blood screening that showed a decrease in colon cancer mortality.

Whether to rate down quality by one or two levels due to indirectness in this context is a matter of judgment. Older trials show a high efficacy of intramuscular penicillin for gonococcal infection, but guidelines might reasonably recommend alternative antibiotic regimes based on current local in vitro resistance patterns, which would not warrant downgrading the quality of evidence for indirectness. Example 6: Interventions not sufficiently different Not Downgraded. Trials of simvastatin show cardiovascular mortality reduction.

Suggesting night rather than morning dosing because of greater cholesterol reduction would not warrant rating down quality for differences in the intervention. Differences in outcomes measures surrogate outcomes. GRADE specifies that both those conducting systematic reviews and those developing practice guidelines should begin by specifying every important outcome of interest. The available studies may have measured the impact of the intervention of interest on outcomes related to, but different from, those of primary importance to patients.

The difference between desired and measured outcomes may relate to time frame e. Another source of indirectness related to measurement of outcomes is the use of substitute or surrogate endpoints in place of the patient-important outcome of interest. Diabetic symptoms, hospital admission, complications cardiovascular, eye, renal, neuropathic. Quality of life, morbidity such as shunt thrombosis or heart failure , mortality. In general, the use of a surrogate outcome requires rating down the quality of evidence by one, or even two, levels.

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Consideration of the biology, mechanism, and natural history of the disease can be helpful in making a decision about indirectness. For surrogates that are far removed in the putative causal pathway from the patient-important endpoints, we would rate down the quality of evidence with respect to this outcome by two levels.

Surrogates that are closer in the putative causal pathway to the outcomes warrant rating down by only one level for indirectness.

Example 7: Time differences in outcomes Downgraded by One Level. A systematic review of behavioral and cognitive-behavioral interventions for outwardly directed aggressive behavior in people with learning disabilities showed that a program of 3-week relaxation training significantly reduced disruptive behaviors at 3 months.

The argument for rating down quality for indirectness becomes stronger when one considers that other types of behavioral interventions have shown an early beneficial effect that was not sustained at 6 months follow-up. Calcium and phosphate metabolism are far removed in the causal pathway from patient-important outcomes such as myocardial infarction, and warrant rating down the quality of evidence by two levels. Surrogate outcomes that are closer in the causal pathway to the patient-important outcomes such as coronary calcification for myocardial infarction, bone density for fractures, and soft-tissue calcification for pain, warrant rating down quality by one level for indirectness.

They found a statistically significant association between progression-free and overall survival in the randomized trials they analyzed, but predicting overall survival using progression-free survival remained uncertain. Rating down quality by one level for indirectness would be appropriate in this situation. Occurs when a comparison of intervention A versus B is not available, but A was compared with C and B was compared with C.

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Such studies allow indirect comparisons of the magnitude of effect of A versus B. As a result of the indirect comparison, this evidence is of lower quality than head-to-head comparisons of A and B would provide. The validity of the indirect comparison rests on the assumption that factors in the design of the trial the patients, co-interventions, measurement of outcomes and the methodological quality are not sufficiently different to result in different effects in other words, true differences in effect explain all apparent differences.

Because this assumption is always in some doubt, indirect comparisons always warrant rating down by one level in quality of evidence. Whether to rate down two levels depends on the plausibility that alternative factors population, interventions, co-interventions, outcomes, and study methods explain or obscure differences in effect.