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Evidence-based Practice |
1 From the Clinical Epidemiology Division, Department of Orthopedic and Trauma Surgery (D.S., K.B., A.E.), and the Institute of Radiology (G.R., S.M.), Unfallkrankenhaus Berlin Trauma Center, Warener Str 7, 12683 Berlin, Germany. Received May 1, 2004; revision requested July 6; revision received July 9; accepted August 15. Address correspondence to D.S. (e-mail: dirk.stengel{at}ukb.de).
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ABSTRACT |
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 TOP ABSTRACT INTRODUCTIONMATERIALS AND METHODSRESULTSDISCUSSIONReferences |
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MATERIALS AND METHODS: Meta-analysis was conducted of prospective investigations in which US was compared with any diagnostic reference test in patients with suspected abdominal injury. Reports were retrieved from electronic databases without language restrictions; added information was gained with manual search. Two reviewers independently assessed methodological rigor by using 27 items contained in the Standards for Reporting of Diagnostic Accuracy (STARD) checklist and the Quality Assessment of Studies of Diagnostic Accuracy included in Systematic Reviews (QUADAS) instrument. Inconsistencies were resolved by means of consensus. Summary receiver operating characteristics and random-effects meta-regression were used to model the effect of methodological standards and other study features on US accuracy.
RESULTS: A total of 62 trials, which included a total of 18 167 participants, were eligible for meta-analysis. The average proportion of men or boys was 71.7%, the mean age was 30.6 years ± 10.8 (standard deviation), and the mean injury severity score was 16.7 ± 8.3. The prevalence of abdominal trauma was 25.1% (95% confidence interval [CI]: 21.1%, 29.1%). Pooled overall sensitivity and specificity of US were 78.9% (95% CI: 74.9%, 82.9%) and 99.2% (95% CI: 99.0%, 99.4%), respectively. Varying end points (hemoperitoneum or organ damage) did not change these results. US accuracy was much lower in children (sensitivity, 57.9%; specificity, 94.3%). Strong heterogeneity was observed in sensitivity, whereas specificity remained constant across trials. There was evidence of publication bias. Initial interobserver agreement with methodological standards ranged from poor (
= 0.03, independent verification of US findings) to perfect ( = 1.00, sufficiently short interval between US and reference test). By consensus, studies fulfilled a median of 13 methodological criteria (range, five to 20 criteria). In investigations that lacked individual methodological standards, researchers overestimated pooled sensitivity, with predicted differences of 9%–18%. The use of a single reference test, specification of the number of excluded patients, and calculation of CIs independently contributed to predicted sensitivity in a multivariate model. In 16 investigations (1309 subjects), a single reference test was used, which provided a combined sensitivity of 66.0% (95% CI: 56.2%, 75.8%).
CONCLUSION: Bias-adjusted sensitivity of screening US for trauma is low. Adherence to methodological standards included in appraisal instruments like STARD and QUADAS is crucial to obtain valid estimates of test accuracy.
Supplemental material: radiology.rsnajnls.org/cgi/content/full/2361040791/DC1
© RSNA, 2005
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INTRODUCTION |
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TOPABSTRACTINTRODUCTIONMATERIALS AND METHODSRESULTSDISCUSSIONReferences |
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Screening ultrasonography (US) for trauma was introduced 30 years ago, when results from a study conducted in Denmark proved it was feasible for use in the discovery of abdominal organ injury (5). After preliminary data were collected, focused abdominal US for trauma (FAST) spread throughout German emergency departments (6) and gradually replaced diagnostic peritoneal lavage.
Reports from the United States showed that US decreased the number of computed tomographic (CT) scans requested in the emergency department (7,8). Moreover, the subcommittee of the American College of Surgeons recently proposed an increased role for FAST examination in advanced trauma life support (9).
Diagnostic algorithms designed for primary trauma survey demand a high level of accuracy. On the other hand, they must keep invasiveness and radiation exposure to the necessary minimum, and US is widely regarded as a method to quickly and easily accomplish these goals. However, it is unclear if certain qualities of the source trials, mainly their methodologic soundness, influenced current estimates of US accuracy.
Several authors proposed checklists to help clinicians distinguish valuable tests from worthless tests (10,11), but there is still no accepted approach to appraise the methodologic rigor of a diagnostic study.
Recently, two promising instruments were introduced to overcome this problem. The Standards for Reporting of Diagnostic Accuracy (STARD) checklist was designed to systematize diagnostic research (12). Quality Assessment of Studies of Diagnostic Accuracy included in Systematic Reviews (QUADAS) was developed to enable researchers to evaluate methodologic issues of individual studies for meta-analyses (13). Thus, the purpose of our study was to evaluate whether compliance with methodologic standards affected the reported accuracy of screening US for trauma.
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MATERIALS AND METHODS |
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TOPABSTRACTINTRODUCTIONMATERIALS AND METHODSRESULTSDISCUSSIONReferences |
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Data gained from this structured search of the scientific literature were combined in a meta-analysis. For simplification, we will use the term FAST+ throughout this article to indicate protocols that target both free fluid and organ injury.
We included reports indexed as prospective investigations, in which patients who had experienced blunt or penetrating abdominal trauma were enrolled and in which US was compared with any diagnostic reference standard. Suitable reference tests included CT, diagnostic peritoneal lavage, laparotomy, clinical observation, outpatient follow-up, or autopsy findings. We retrieved peer-reviewed scientific material, as well as abstract presentations, book chapters, and gray literature (ie, non–peer-reviewed material, press releases, and presentations) that were available on the Internet. Animal studies, technical investigations, and case reports were excluded from this review.
Search Strategy
Three authors (D.S., K.B., G.R.) conjointly searched the MEDLINE, EMBASE, and CINAHL databases and the Cochrane Central Register of Controlled Trials, beginning with the first citation of diagnostic US and ending with January 2004. Table E1, which is available as supplemental material on the Radiology Web site (radiology.rsnajnls.org/cgi/content/full/2361040791/DC1), details our MEDLINE and EMBASE search strategy with medical subject headings, Emtree keywords, and free-text items.
An Internet search was conducted by using Google. We also used the search engine of the Radiological Society of North America (available at: www.radiology.rsnajnls.org), which serves Radiology and RadioGraphics. The Lippincott Williams and Wilkins Web site (available at: www.lww.com) allowed for comprehensive searching of the Journal of Trauma and Annals of Surgery back to 1996. Other relevant periodicals were traced with the Springer Web site (available at: www.springerlink.com). No restrictions applied to language.
In accordance with the Cochrane method, we collected a first set of potentially eligible articles after scrutinizing the title or abstract. In case of vague, insufficient, or conflicting information, we retrieved the full text of articles.
Two reviewers (D.S., K.B.) cross-referenced bibliographies of all original manuscripts for publications not identified with the electronic search and manually searched all journal issues containing the study of interest for other relevant investigations.
Data Collection
Two reviewers (D.S., K.B.) independently extracted information on a data abstraction sheet. We assessed publication language, year, recruitment periods, sample sizes, demographic details, and injury severity. We recorded features of the index test (eg, transducer types, video or hard-copy storage of images, interpretation of US images by surgeons or radiologists) and the diagnostic reference standard or standards used in individual trials.
The abstraction form listed items and subitems of STARD (original tool, 25 items) and QUADAS (14 items) that referred to the Materials and Methods section and the Results section of individual articles. Accounting for some items included in both instruments, two researchers (D.S. and K.B.) selected 27 methodologic standards (22 of which can be found in STARD, and 14 of which are contained in QUADAS) for evaluation of methodologic quality (Table 1).
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In particular, appropriateness of the reference test and outcome definitions were investigated. According to QUADAS, a proper reference standard is likely to allow physicians to classify the target disease correctly. Discussion between the surgeons (D.S. and K.B.) and the radiologists (G.R. and S.M.) left CT as the imaging standard of choice, demanding sufficient information on conventional or helical examination techniques and application of intravenous or oral contrast agents. Accepted invasive verification procedures were diagnostic peritoneal lavage, laparotomy, laparoscopy, or autopsy.
Three authors (D.S., K.B., and A.E.) agreed on clinical observation as a suitable reference test if authors detailed the number of patients hospitalized and discharged, time of surveillance, or the interval between physical examinations.
We considered detection of free intraabdominal fluid, organ injury, or both to be satisfactory definitions of CT and US results. Also, proper classification of disease was assigned for exact descriptions of diagnostic peritoneal lavage findings (eg, a red blood cell count of more than 100 000 per cubic millimeter [1 x 1012/L] of fluid).
We considered board-certified radiologists to be experts in the performance of US and interpretation of US findings. If surgeons conducted US examinations, we assumed expertise if operators had attended formal training lessons or were supervised by an expert in US.
Statistical Analysis
After independent data abstraction and rating of studies, we calculated statistics to assess interobserver agreement beyond chance. After completion of independent ratings, two authors (D.S. and K.B.) resolved inconsistencies in consensus and discussed areas of concern with others (G.R., S.M., and A.E.). Secular changes in the number of fulfilled methodologic standards were evaluated with unweighted linear regression analysis.
For each study, we calculated descriptive statistics (sensitivity, specificity, and likelihood ratios) with their 95% CIs. Summary receiver operating characteristic curves were obtained by using the method of Moses et al (14).
We used Hasselblad diagnostic d (the standardized distance between the means of the healthy patients and those with disease) as a global measure to discover publication bias (15,16). We used the Egger regression method to test for funnel plot asymmetry (17).
A plot of sample size versus treatment effect should be shaped like a funnel if there is no publication bias. If the number of studies in which small effect sizes are found is lacking because these reports have less chance of being published, the plot will become skewed. Publication bias is assumed if the intercept of the regression line fitted through the data cloud of standardized effects versus precision is significantly away from zero. Statistical heterogeneity was explored by using a Galbraith diagram (18,19).
In a plot of standardized effect measures (that is, the point estimate divided by its standard error) against inverse standard errors, a homogeneous set of trials will scatter with constant variance along a regression line fitted through the data cloud. Trials situated beyond two standard errors of this line substantially contribute to statistical heterogeneity. In addition, we calculated Cochran Q as an estimate of heterogeneity with the diagnostic odds ratio (18). Q is 
2 distributed with k minus one degree of freedom, where k is the number of studies included in the meta-analysis. As a rule of thumb, statistical heterogeneity is assumed if Q exceeds the number of studies.
We applied random-effects meta-regression with restricted maximum likelihood estimation to combine sensitivity and specificity and to examine sources of heterogeneity in the data set (20,21). Controversy exists as to the value of quality scores. We followed recommendations and tested the influence of individual quality standards on outcomes rather than sum scores (22,23).
Preferentially, we determined the effect of individual methodologic standards, patient risk profiles (eg, age, sex, and injury severity), and other study features (eg, transducer type and surgeon or radiologist operators) on test accuracy.
Variables that significantly affect test accuracy in the univariate analysis (P < .25) were included in a multivariate meta-regression model (24). We used a stepwise selection procedure and excluded variables with a P value of more than .1.
The final model was selected on the basis of the degree of unexplained variance, as marked by 
2, which decreases with better model fit (18). In contrast to postregression diagnosis with traditional methods, indicators of model fit like R2 or the Akaike Information Criterion are not available with the mixed model extension used for meta-analysis. We used Stata Release 8.0 software (Stata, College Station, Tex) for all analyses.
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RESULTS |
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TOPABSTRACTINTRODUCTIONMATERIALS AND METHODSRESULTSDISCUSSIONReferences |
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Most articles were published in English (n = 56, 90.3%). On average, 71.7% of subjects in the studies were men or boys (95% CI: 68.5%, 74.9%). Mean age was 30.6 years (95% CI: 27.6%, 33.7%). Average injury severity score was 16.7 (95% CI: 13.1%, 20.3%), which indicates that many patients had multiple injuries. In 50 studies, patients with suspected blunt abdominal injury were enrolled. Ten other studies included varying but still moderate numbers of subjects with stab and gunshot wounds (average proportion, 11.7%; 95% CI: 4.6%, 18.7%), whereas two studies included only patients with penetrating trauma.
A list of studies excluded from this systematic review is available from the authors on request.
Quality Assessment
Most investigations fulfilled a grade B recommendation for diagnostic studies. This included studies meeting level 2b (ie, exploratory cohort study with good reference standards) and level 3b (ie, nonconsecutive study or study without consistently applied reference standards) evidence.
In one study, researchers explored diagnostic accuracy of US in the experimental arm of a randomized trial (therapeutic interventions: level Ib evidence, grade A recommendation). The aim of this study was to investigate the effectiveness of US-based clinical pathways to reduce the number of requested CT examinations.
In two other studies, researchers addressed similar outcomes by using a quasi-randomized format (allocating patients by date or time of admission), which is currently not explicitly covered by the available grading schemes.
During early appraisal, two authors (D.S. and K.B.) disagreed about the presence of work-up bias if clinical follow-up examinations were used as the sole confirmation procedure. This also influenced their ratings of the appropriateness of the reference standard to classify the target disease.
In several articles, it was unclear whether all subjects with negative findings at US who did not undergo further imaging studies were admitted to the hospital or deliberately followed as outpatients. K.B. found no exact statements regarding the follow-up policy in 12 (19.4%) reports, whereas D.S. suspected 31 (50.0%) studies did not aim at independent clinical surveying.
All authors agreed that statements such as, "all patients in this study were observed for 72 hours" (26), "patients were observed in a holding area for 4–6 hours and discharged at the discretion of the attending surgeon" (27), or "patients had follow-up as outpatients" (28) indicated independent confirmation of US findings. A reappraisal of all studies involving a third reviewer (G.R.) left 21 (33.9%) investigations without description of clinical follow-up rules in case of a negative US finding.
In addition, D.S. and K.B. dissented on the true prospective design of some investigations. After consensus was reached, methods of data collection remained ambiguous in 11 (17.7%) studies. Table 2 summarizes the proportion of methodologic standards fulfilled by the study pool and the interobserver agreement achieved during independent rating. A representative spectrum of patients was covered by all but one study, which used a quasi-case control design (level 4 evidence, grade C recommendation) (29).
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Altogether, studies satisfied a median of 13 methodologic standards (range, five to 20 standards). Of 14 items contained in QUADAS and 22 items listed in STARD, studies fulfilled a median of seven items (range, two to 10 items) and 12 items (range, four to 17 items), respectively.
There was a rising trend in the number of studies meeting standards during the publication period (ie, from 1982 to 2003). Predicted annual increases in the number of items were 0.313 for the entire catalog (P = .001), 0.305 for STARD (P < .001), and 0.173 for QUADAS (P = .003).
Assessment of Publication Bias and Statistical Heterogeneity
Funnel plot analysis provided evidence of publication bias (intercept, 1.06; 95% CI: –0.27, 2.39) (slope, 2.29; 95% CI: 1.83, 2.75) (P < .001), with better test performance found in smaller studies (Fig 2).
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2, 314.3; P < .001). Specificity was remarkably constant across studies, with only one investigation located below the margin of 2 standard errors. In contrast, sensitivity ranged from 30.8% to 100.0%, with at least 17 investigations substantially contributing to heterogeneity.
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Meta-Analysis
The prevalence of abdominal injury (organ damage, free fluid, or both) was, on average, 25.1% (95% CI: 21.1%, 29.2%). Overall sensitivity and specificity of US was estimated at 78.9% (95% CI: 74.9%, 82.9%) and 99.2% (95% CI: 99.0%, 99.4%).
There was no significant difference in test characteristics between FAST and FAST+ investigations (Fig 4). Pooled sensitivities were 77.8% (95% CI: 72.1%, 83.5%) and 80.3% (95% CI: 74.7%, 85.9%), whereas pooled specificities were 99.4% (95% CI: 99.2%, 99.6%) and 98.9% (95% CI: 98.5%, 99.5%), respectively. Few reports detailed the ability of US to depict hepatic or splenic tears, which suggests sensitivities of 66.5% and 62.6% and specificities of 97.2% and 96.6%, respectively.
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Nine trials (involving a total of 905 patients) included children with a mean age of 9.6 years ± 3.5 (standard deviation) and show unexpectedly low accuracy of US when compared with the general population. Pooled sensitivity was only 57.9% (95% CI: 44.9%, 70.9%), whereas combined specificity was 94.3% (95% CI: 90.1%, 98.5%). This mainly reflected strict adherence to methodologic standards (eg, single well-described confirmation procedures and blinded reading of both index and reference tests). Studies of children met a median of 17 methodologic criteria (range, six to 19 criteria). Figure 6 displays the related summary receiver operating characteristics.
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Table 2 summarizes associations between methodologic standards and predicted sensitivity gained from meta-regression.
Methodologic rigor had a major effect on accuracy estimates, and it confounded all further calculations. Studies missing certain design features yielded higher sensitivity than did investigations with stricter adherence to methodologic standards.
With univariate analysis, issues related to the choice of the particular reference test substantially influenced sensitivity, as did blinding and accurate reporting of patient flow (that is, specification of the number of screened patients and those who later dropped out).
Table 3 summarizes other variables that influenced sensitivity (eg, publication language, proportion of male subjects, mean age of the study population, proportion of CT scans, frequency of US probes, and area of expertise of operators). There was a slight association between predicted sensitivity and injury severity scores; however, data could be abstracted from only 23 investigations.
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No investigation fulfilled all of these standards. Pooled sensitivity of 16 studies (that included a total of 1309 participants) that verified US findings with a single reference test was only 66.0% (95% CI: 56.2%, 75.8%), compared with 83.2% (95% CI: 79.5%, 86.9%) in case of multiple reference tests.
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DISCUSSION |
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TOPABSTRACTINTRODUCTIONMATERIALS AND METHODSRESULTSDISCUSSIONReferences |
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In this study, we used a searching algorithm that was far more sensitive than that used in our previous study. This study also included nearly twice as many investigations. We arrive at the same conclusions; that is, a sonogram that is positive for fluid or organ damage is decisive, whereas a negative sonogram is not. However, this study provides more detailed insight into the distribution of effect measures, and it contributes empirical evidence of the size and direction of design-related bias (33). It is open to debate whether the present results are confined to the issue of trauma US, or if they might suit diagnostic test research in general. There is no accepted hierarchy of validity criteria, and it is simply not reasonable to assign levels of universal importance to methodologic features. Standards that influence the accuracy of a particular test may not apply to another.
As a common finding of meta-analyses, methodologic quality of the original studies was, at best, average. Those who perform meta-analysis are often blamed for monotonously criticizing study quality. There is no real alternative available to caregivers; therefore, they must use the best available scientific data and take its possible limits into account.
Of note, after correcting for methodologic drawbacks, pooled sensitivity of trauma US settled close to 65% compared with a combined sensitivity of 80% projected from the entire pool of studies. Assuming a constantly high specificity of around 99%, corrections for bias shift negative likelihood ratios from 0.20 to 0.35. In other words, quality-adjusted estimates of test accuracy suggest minor changes in the pretest probability of abdominal trauma by negative US results (34).
Although perfect specificity is desirable for a screening tool to avoid unnecessary additional tests, it must provide high sensitivity so that a certain condition is not missed. One might ask whether a screening test that fails to lead to recognition of 11% of patients with abdominal injury is helpful in clinical practice.
Several points of our meta-analysis merit further discussion. First, application of the STARD checklist as a measure of methodologic rigor is beyond its intended use. The STARD steering committee admitted the limited evidence of linking particular items to potential bias (12).
Most suggestions provided by STARD match the methodologic norms included in QUADAS and show that they consistently affect accuracy estimates. Nevertheless, the expanded use of STARD may have introduced artificial relationships. For example, it is not obvious why providing measures of numerical precision independently affected sensitivity. We interpreted CIs as a surrogate of consequential planning, accomplishment, and analysis of the particular study. We cannot, however, exclude a false-positive correlation due to chance.
Clearly, bad reporting does not necessarily mean bad performance of a study (35). We did not contact authors, which might have clarified some controversies. We tried to contact researchers during our preceding review, but we were unable to obtain unpublished information.
Second, interobserver agreement ranged from poor to almost perfect. Although reviewers consistently agreed on items that later significantly affected test sensitivity, different ideas of bias related to certain design features might influence the external validity of our results.
Assessing retest reliability or internal consistency (usually measured with Cronbach 
) of STARD or QUADAS was beyond the scope of this study. The inconsistency in ratings may point to the limited utility of these appraisal tools and should prompt further investigation.
Third, we restricted our search to prospective investigations, which ignore important evidence from reviews of trauma registries. We hypothesized that data collection according to a prospectively defined protocol minimizes misclassification of exposure and disease. However, prospective patient sampling did not influence sensitivity in the meta-regression model, and it may be of minor importance if authors respect other methodologic key items.
Sirlin et al (36) recently published an excellent retrospective review of a huge trauma database. The study was extensive and provided high internal validity. Among 4000 patients who fulfilled the entry criteria for the multiple trauma outcomes study, 3641 had true-negative US findings, whereas 38 had false-negative findings.
Sirlin et al (36) infer from their data that negative findings at screening US have high clinical value. We think that this interpretation is problematic. US produced a high negative predictive value (99%), which is not surprising given the low prevalence of abdominal injury in the studied population (with a maximum of 9%, if one assumes there were no false-positive findings). The published data comply with a range in US sensitivity of 0% to 89% (if all 321 positive sonograms had been either false-positive or true-positive) and a range in US specificity of 92% to 100% (assuming opposite scenarios). These test characteristics compare well with those noted in this meta-analysis, further centering the projected point estimates.
Excluding citations after judging titles or abstracts bears the risk of omitting potentially relevant work. We adhered to accepted methods to avoid this bias, however, there is little empirical evidence on the possible effect of falsely neglected studies on the findings of a meta-analysis.
US findings must always be interpreted in the clinical context (36). The likelihood of intraabdominal disasters depends on the physical condition at arrival and the presence of index or multiple injuries. As a convenient means for scheduled bedside examinations, US may objectify progressive bleeding in case of clinical worsening. The available data did not allow for a more detailed analysis of the accuracy of serial scans, which may represent a major, if not the only, advantage of US over CT.
Regardless of US findings, hemodynamically stable patients will almost always undergo CT scanning before they are transferred to the intensive care unit. This is reasonable since a negative sonogram is not convincing, whereas a positive sonogram is definite and warrants both organ injury scaling and exclusion of accompanying injury. US contributes little to decision making in these subjects. In hypotensive patients, because of its unsatisfactory sensitivity, a negative sonogram hardly decreases the high prior probability of intraabdominal injury and impels enforcement of the correct diagnosis by definite standards.
Several authors (37–39) emphasized the prognostic importance of increasing quantities of fluid and the ability of US scores to signal the need for therapeutic laparotomy. One might speculate that a continuous or ordinal classification of hemoperitoneum, rather than a dichotomous classification, improves the receiver operating characteristics of FAST.
On the other hand, other researchers (40,41) stressed the lack of free intraabdominal fluid as a limit of screening US. The prevalence of organ tears without accompanying hemoperitoneum occasionally exceeds 35% (42). Also, US rarely depicts hollow viscus rupture. This entity clearly remains a domain of CT scanning (43,44).
With continuing developments in CT technology, such as fast multi–detector row CT scanners that are almost at the initial point of care and skilled interdisciplinary critical care teams, there are now few subjects whose medical condition precludes definite diagnostic imaging in a reasonable time frame (45–47).
The possible benefits of emergency US are confined to patients with refractory hypotension and positive findings. Many protocols excluded potentially eligible patients who, by clinical judgment alone, required laparotomy without delay. Obviously, this would have increased rather than decreased the number of true-positive findings; however, it cannot be tested on a grand scale because the number of excluded subjects was rarely disclosed.
It is unclear how much importance doctors assign to a predictably positive sonogram in their decision to perform surgery in hypotensive patients with a high prior probability of abdominal trauma. Fryback and Thornbury (48) proposed six factors to consider in the appraisal of diagnostic test research: (a) technical measures, (b) accuracy, (c) influence on diagnostic thinking (that is, the difference between prior and posterior odds of disease), (d) influence on therapeutic decisions, (e) patient outcome, and (f) societal benefits.
The third factor is of interest in US-guided emergency laparotomy. In a decision analysis report, Brown et al (49) showed a linear decrease in the expected utility of US with rising prevalence of intraabdominal injury. This supports the thesis of a reassuring rather than an essential role of US findings in inducing further actions.
Meta-analyses are valuable instruments with which to generate theories. Because of their retrospective nature, however, they cannot be used to prove hypotheses. Variations in the individual prevalence of abdominal injury, local differences in trauma algorithms, and heterogenous source populations increase the risk of comparing apples with oranges. Obviously, multivariate random-effects modeling of published information reduced but did not fully dissolve the degree of unexplained variance. Demographic details and other important study features that might have contributed to heterogeneity were only partially available. Thus, we had limited choices in building hierarchical models on variables other than methodologic standards (eg, transducer frequency and operator expertise).
Researchers who are planning to conduct a diagnostic study must deal with various systematic errors and proper methods to minimize them efficiently. The same applies to the reader of a scientific article who wants to appraise the validity of the published results. A detailed assessment of methodologic strengths, as guided by the STARD checklist or the QUADAS instrument, may affect conclusions drawn from studies of diagnostic test accuracy. Referring to US performed to assess abdominal trauma, our data warrant additional research on topics like serial examinations, quantitative sensitivity, different end points, and influence of operator expertise, including proper methods to corroborate US findings.
The future reputation of US in the assessment of abdominal trauma will depend on the methodologic rigor of investigations currently under way.
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ACKNOWLEDGMENTS |
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FOOTNOTES |
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Abbreviations: CI = confidence interval • FAST = focused abdominal ultrasonography for trauma • QUADAS = Quality Assessment of Studies of Diagnostic Accuracy included in Systematic Reviews • STARD = Standards for Reporting of Diagnostic Accuracy
Authors indicated no financial relationship to disclose.
Author contributions: Guarantor of integrity of entire study, D.S.; study concepts and design, D.S., K.B.; literature research, D.S., K.B., G.R.; data acquisition, D.S., K.B., G.R.; data analysis/interpretation, all authors; statistical analysis, D.S.; manuscript preparation, D.S., K.B.; manuscript definition of intellectual content, all authors; manuscript editing, D.S.; manuscript revision/review and final version approval, all authors
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References |
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TOPABSTRACTINTRODUCTIONMATERIALS AND METHODSRESULTSDISCUSSIONReferences |
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). 
= predictions adjusted for the number of methodologic standards.