Source: Trasande L, Attina T, Trachtman H, et al. Bisphenol A exposure is associated with low-grade urinary albumin excretion in children of the United States. Kidney Int. 2013;83(4):741-748; doi:10.1038/ki.2012.422. See AAP Grand Rounds commentary by Dr. Christine Sethna (subscription required).
PICO Question: Among children in the United States, is urinary bisphenol A associated with urinary albumin excretion?
Question type: Causation
Study type: Cross-sectional
Last summer, the FDA banned the use of polycarbonate resins, such as bisphenol-A (BPA), in infant formula bottles and sippy cups. However, the reason for this action, as noted in the Federal Register statement, was based on the principle of abandonment, rather than via any clear cut evidence of health risks. Abandonment simply means that manufacturers have already quit using BPAs in these products. Determining health risks of environmental compounds is a real quagmire; in general, most evidence is collected via case control or other retrospective study designs, which don't allow for assessment of causation and only can demonstrate an association of an exposure with a particular outcome of interest.
The present study is a good example of two features in evidence-medicine to consider when advising patients and families about risks. First, this study looked at a surrogate outcome, urinary albumin-to-creatinine ratio (ACR), which might be an indicator of renal endothelial dysfunction and theoretically lead to early atherosclerosis. This is called a surrogate outcome (or biomarker in some circles) whereby ACR serves as a proxy for an outcome that is more important to patients, such as atherosclerosis. Of course, even atherosclerosis is a surrogate outcome, but the link from atherosclerosis to heart attacks and other causes of morbidity and mortality is quite strong, unlike the link from ACR to atherosclerosis. So, it's a bit of a leap of faith to say increased ACR is a bad thing (not to mention how much of an increase is important), but it's unlikely to be a good thing.
Which brings me to the second feature that is ultimately more interesting and difficult to address, yet it's something physicians do every day. How do we advise our patients and families on proper preventive health measures when the evidence is either weak or nonexistent? An absence of high quality evidence shouldn't paralyze us into inaction, but rather explain the situation to our patients and offer choices and recommendations. In the case of BPA in containers and foods, I'd point to a statement in the discussion section of the study: "... in the absence of definitive evidence to confirm the hazards of BPA[,] proactive and precautionary advice to limit exposure may be of benefit." In other words, avoid BPA if you can, especially for young children. At least we don't have the newer baby bottles and sippy cups to worry about in the US, thanks to the abandonment principle!
The Pediatric Environmental Health Specialty Units are a great general resource for the lay public as well as for health professionals.
Sunday, May 19, 2013
Sunday, May 12, 2013
Getting From Evidence to Action
Source: Eckrich MJ, Wang WC, Yang E, et al. Adherence to transcranial Doppler screening guidelines among children with sickle cell disease. Pediatr Blood Cancer. 2013;60(2):270-274; doi:10.1002/pbc.24240. See AAP Grand Rounds commentary by Dr. Onyinye Onyekwere (subscription required).
PICO Question: Among children with severe sickle cell disease, what percentage have received a transcranial Doppler ultrasound according to screening guidelines and what are the factors that influence adherence?
Question type: Descriptive
Study design: Retrospective cohort
Why do patients fail to receive healthcare interventions that have been shown to provide clear benefit? Moving from evidence in clinical trials to taking the action of implementing improvements in healthcare is perhaps the most neglected aspect of evidence-based medicine, but clearly the most important. In the current study, investigators looked at patients with sickle cell or sickle beta thalassemia disease who were enrolled in Tennessee Medicaid and received care at either of two large sickle cell centers in Tennessee. Transcranial Doppler ultrasonography (TCD) screening of children with sickle cell disease strongly predicts those at risk for stroke. Between 1997, when the recommendations for TCD for children 2-16 years of age first appeared, to 2008, a little over two-thirds of 338 at-risk children had at least one TCD, and about the same percentage received the recommended annual screening. Why wasn't it closer to 100%?
One possible reason could be that clinicians were unaware of the recommendations. The NIH document, "The Management of Sickle Cell Disease" and the AAP guideline on "Health Supervision for Children with Sickle Cell Disease" both include discussion of TCD screening for these children, but neither utilizes strength of evidence ratings, and the AAP guidelines mention TCD as one in a list of options for screening "if indicated," but it's perhaps a little vague on the indications. If I were reading the guidelines as a general pediatrician, this wouldn't come across as a strong recommendation to me. However, the current study looked at children receiving care in large sickle cell centers where I think the clinicians would be both highly aware of and highly motivated to utilize TCD screening.
The study mostly looked at other factors associated with adherence to the recommendations, and found that children whose mothers had at least a high school education and children with more outpatient visits at the centers were more likely to have TCD screening. As Dr. Onyekwere notes in her commentary, interventions such as better patient and family education, follow-up of missed appointments, and perhaps tightening of protocols in sickle cell disease clinics to track TCD use may get us closer to the 100% number. When you think about it, those are relatively minor (and inexpensive) interventions to put good evidence into action.
PICO Question: Among children with severe sickle cell disease, what percentage have received a transcranial Doppler ultrasound according to screening guidelines and what are the factors that influence adherence?
Question type: Descriptive
Study design: Retrospective cohort
Why do patients fail to receive healthcare interventions that have been shown to provide clear benefit? Moving from evidence in clinical trials to taking the action of implementing improvements in healthcare is perhaps the most neglected aspect of evidence-based medicine, but clearly the most important. In the current study, investigators looked at patients with sickle cell or sickle beta thalassemia disease who were enrolled in Tennessee Medicaid and received care at either of two large sickle cell centers in Tennessee. Transcranial Doppler ultrasonography (TCD) screening of children with sickle cell disease strongly predicts those at risk for stroke. Between 1997, when the recommendations for TCD for children 2-16 years of age first appeared, to 2008, a little over two-thirds of 338 at-risk children had at least one TCD, and about the same percentage received the recommended annual screening. Why wasn't it closer to 100%?
One possible reason could be that clinicians were unaware of the recommendations. The NIH document, "The Management of Sickle Cell Disease" and the AAP guideline on "Health Supervision for Children with Sickle Cell Disease" both include discussion of TCD screening for these children, but neither utilizes strength of evidence ratings, and the AAP guidelines mention TCD as one in a list of options for screening "if indicated," but it's perhaps a little vague on the indications. If I were reading the guidelines as a general pediatrician, this wouldn't come across as a strong recommendation to me. However, the current study looked at children receiving care in large sickle cell centers where I think the clinicians would be both highly aware of and highly motivated to utilize TCD screening.
The study mostly looked at other factors associated with adherence to the recommendations, and found that children whose mothers had at least a high school education and children with more outpatient visits at the centers were more likely to have TCD screening. As Dr. Onyekwere notes in her commentary, interventions such as better patient and family education, follow-up of missed appointments, and perhaps tightening of protocols in sickle cell disease clinics to track TCD use may get us closer to the 100% number. When you think about it, those are relatively minor (and inexpensive) interventions to put good evidence into action.
Sunday, May 5, 2013
IV acetaminophen
Source: Ceelie I, de Wildt SN, van Dijk M, et al. Effect of intravenous paracetamol on postoperative morphine requirements in neonates and infants undergoing major noncardiac surgery: a randomized controlled trial. JAMA. 2013;309(2):149-154; doi:10.1001/jama.2012.148050. See AAP Grand Rounds commentary by Dr. Jennifer Workman (subscription required).
PICO Question: Among infants who have had major surgery, does intermittent IV acetaminophen decrease the need for morphine?
Question type: Intervention
Study design: Randomized controlled
This study was pretty well done as studies go: randomized, double-blind, clear-cut primary outcome measure (number of morphine doses needed to manage pain in addition to the study drug), plus some secondary outcomes that patients and families would care about more directly such as pain scores and morphine-related side effects. Bottom line, for major abdominal and non-cardiac thoracic surgery in neonates and infants under 1 year of age, IV acetaminophen was better than continuous IV morphine infusion for postoperative pain management by an impressive margin.
The interesting part of this study for me is deciding where the results fit in with clinical care. Stated differently, should clinicians managing pain in young infants make the switch to IV acetaminophen? First, from a practical standpoint it doesn't really matter, since IV acetaminophen isn't available in the US in a usable dosage form. Even if it weren't a problem, however, this excellent study still wouldn't clear that high bar.
First, for an excellent discussion of the numerous physiologic and developmental issues surrounding pain, opioids, and acetaminophen use in infants, read the excellent editorial on opiophobia. From a purely study design standpoint, however, note that this study took place at a single center and evaluated only 71 children in total. The study enrollment criteria were very explicit (a good thing), but of course might limit generalizability of the results to children in different circumstances following surgery.
An ongoing trial of IV acetaminophen for infants up to 2 years of age with postoperative or acute traumatic pain relief will complete data collection in June 2014. It is a multicenter study at 8 US tertiary care centers. These results, if favorable, might tip the scales in favor of adopting IV acetaminophen use for infants.
PICO Question: Among infants who have had major surgery, does intermittent IV acetaminophen decrease the need for morphine?
Question type: Intervention
Study design: Randomized controlled
This study was pretty well done as studies go: randomized, double-blind, clear-cut primary outcome measure (number of morphine doses needed to manage pain in addition to the study drug), plus some secondary outcomes that patients and families would care about more directly such as pain scores and morphine-related side effects. Bottom line, for major abdominal and non-cardiac thoracic surgery in neonates and infants under 1 year of age, IV acetaminophen was better than continuous IV morphine infusion for postoperative pain management by an impressive margin.
The interesting part of this study for me is deciding where the results fit in with clinical care. Stated differently, should clinicians managing pain in young infants make the switch to IV acetaminophen? First, from a practical standpoint it doesn't really matter, since IV acetaminophen isn't available in the US in a usable dosage form. Even if it weren't a problem, however, this excellent study still wouldn't clear that high bar.
First, for an excellent discussion of the numerous physiologic and developmental issues surrounding pain, opioids, and acetaminophen use in infants, read the excellent editorial on opiophobia. From a purely study design standpoint, however, note that this study took place at a single center and evaluated only 71 children in total. The study enrollment criteria were very explicit (a good thing), but of course might limit generalizability of the results to children in different circumstances following surgery.
An ongoing trial of IV acetaminophen for infants up to 2 years of age with postoperative or acute traumatic pain relief will complete data collection in June 2014. It is a multicenter study at 8 US tertiary care centers. These results, if favorable, might tip the scales in favor of adopting IV acetaminophen use for infants.
Wednesday, May 1, 2013
The May 2013 Lineup
Hello All,
Things are heating up for the summer, and the new issue of AAP Grand Rounds is hot off the presses. Look up the interesting reviews on topics such as risk of fetal death with influenza versus influenza vaccine (no surprise here!), an association between tooth agenesis and malignant disease, speech and behavior problems in children with DiGeorge syndrome, and more.
In the coming Sundays, I'll be adding my rants on IV acetaminophen for pain control following infant surgery, stroke screening in sickle cell disease children, renal effects of bisphenol A (that controversial ingredient in food and beverage containers), and use of bracing for chest wall deformities. I hope you'll join me.
Things are heating up for the summer, and the new issue of AAP Grand Rounds is hot off the presses. Look up the interesting reviews on topics such as risk of fetal death with influenza versus influenza vaccine (no surprise here!), an association between tooth agenesis and malignant disease, speech and behavior problems in children with DiGeorge syndrome, and more.
In the coming Sundays, I'll be adding my rants on IV acetaminophen for pain control following infant surgery, stroke screening in sickle cell disease children, renal effects of bisphenol A (that controversial ingredient in food and beverage containers), and use of bracing for chest wall deformities. I hope you'll join me.
Sunday, April 28, 2013
Massaging the Data
Source: Ang JY, Lua JL, Mathur A, et al. A randomized placebo-controlled trial of massage therapy on the immune system of preterm infants. Pediatrics. 2012;130(6):e1549-e1558; doi:10.1542/peds.2012-0196. See AAP Grand Rounds commentary by Dr. John Mark (subscription required).
PICO Question: In stable premature infants, does massage therapy improve immune function?
Question type: Intervention
Study design: Randomized controlled
I learned a great deal from this article and from Dr. Mark's excellent commentary. Dr. Mark points out that massage therapy for premature infants has a considerable evidence base, including a Cochrane review suggesting that this intervention may result in improved weight gain, shorter hospitalization and fewer complications, and slightly improved developmental testing scores (though they note some problems with reliability of these findings).
The current study looked at 120 infants in the Hutzel Women's Hospital NICU in Detroit, with about half randomized to a standardized massage therapy intervention and the other half receiving no intervention; caregivers were blinded as to group assignment by having research nurses perform the intervention, or placebo, behind screening curtains. I'm hoping the research nurses weren't moonlighting or otherwise providing care to these newborns, because that might jeopardize the study blinding, but the authors didn't state whether this could have occurred. Also noteworthy is that this study included only the healthiest prematures, and because immune function was being studied, they didn't allow infants who had received steroid therapy or breast milk to be enrolled. So, whatever results ensue, we have a large group of premature infants who weren't studied and might have different results with massage therapy.
The primary study aim was to assess the impact of the intervention on NK cell numbers. The researchers also reported on a number of other outcomes. Bottom line: no proportional increase in numbers of NK cells between the two groups, although mean NK cell cytotoxicity and weight gain were better in the infants receiving massage. In looking at the exact numbers for the mean NK cytotoxicity, I have questions as to whether the difference would be clinically significant, regardless of statistical significance. Also, I've stated in this blog in the past that reporting just group means is not particularly helpful in determining potential impact of a treatment; I would want to know how many infants in each group achieved a cytotoxicity level that would be deemed "normal" or likely to be clinically helpful, and the authors don't provide us with that information. In this study, I'm more intrigued by the weight gain, but even this improvement didn't appear to result in shorter hospitalizations.
I could use a good back rub after digesting all this information. I still have some doubts as to the overall benefit of massage therapy in premature infants, and I would put this study in the category of interesting, but not ready for prime-time implementation without further research.
PICO Question: In stable premature infants, does massage therapy improve immune function?
Question type: Intervention
Study design: Randomized controlled
I learned a great deal from this article and from Dr. Mark's excellent commentary. Dr. Mark points out that massage therapy for premature infants has a considerable evidence base, including a Cochrane review suggesting that this intervention may result in improved weight gain, shorter hospitalization and fewer complications, and slightly improved developmental testing scores (though they note some problems with reliability of these findings).
The current study looked at 120 infants in the Hutzel Women's Hospital NICU in Detroit, with about half randomized to a standardized massage therapy intervention and the other half receiving no intervention; caregivers were blinded as to group assignment by having research nurses perform the intervention, or placebo, behind screening curtains. I'm hoping the research nurses weren't moonlighting or otherwise providing care to these newborns, because that might jeopardize the study blinding, but the authors didn't state whether this could have occurred. Also noteworthy is that this study included only the healthiest prematures, and because immune function was being studied, they didn't allow infants who had received steroid therapy or breast milk to be enrolled. So, whatever results ensue, we have a large group of premature infants who weren't studied and might have different results with massage therapy.
The primary study aim was to assess the impact of the intervention on NK cell numbers. The researchers also reported on a number of other outcomes. Bottom line: no proportional increase in numbers of NK cells between the two groups, although mean NK cell cytotoxicity and weight gain were better in the infants receiving massage. In looking at the exact numbers for the mean NK cytotoxicity, I have questions as to whether the difference would be clinically significant, regardless of statistical significance. Also, I've stated in this blog in the past that reporting just group means is not particularly helpful in determining potential impact of a treatment; I would want to know how many infants in each group achieved a cytotoxicity level that would be deemed "normal" or likely to be clinically helpful, and the authors don't provide us with that information. In this study, I'm more intrigued by the weight gain, but even this improvement didn't appear to result in shorter hospitalizations.
I could use a good back rub after digesting all this information. I still have some doubts as to the overall benefit of massage therapy in premature infants, and I would put this study in the category of interesting, but not ready for prime-time implementation without further research.
Sunday, April 21, 2013
Kawasaki Disease: Algorithm, Cookbook, or Neither
Source: Ling XB, Kanegaye JT, Ji J, et al. Point-of-care differentiation of Kawasaki disease from other febrile illnesses. J Pediatr. 2013;162(1):183-188; doi:10.1016/j.jpeds.2012.06.012. See AAP Grand Rounds commentary by Dr. Robert Tolan, Jr. (subscription required).
PICO Question: Among febrile children can a clinically useful algorithm differentiate Kawasaki disease from other febrile illness?
Question type: Diagnosis
Study design: Prospective cohort
Hardly a week goes by in my practice that I don't make the comment, "I hate Kawasaki Syndrome.*" I hate it because it's a very tricky diagnosis, one that ultimately we can never be certain about unless the child develops true coronary artery aneurysms. (I have my doubts about whether the finding of coronary ectasias, a subtler finding on echocardiogram, is clinically significant or unique to KS.)
So, I'm highly interested in studies aiming to improve diagnostic capabilities for KS. This study, from Stanford and UCSD, has a novel approach and is worth reading, even though the findings don't offer an immediate boost to patient care capabilities. Two tweaks to the usual diagnostic algorithm approach distinguish this study: 1) the authors utilized a sophisticated computerized system to "train" a scoring system based on clinical, laboratory, and combined data with repetitive modeling of receiver operating characteristic (ROC) curves (quick explanation: it provides a graphical view of tradeoffs between sensitivity and specificity of tests); 2) they have made their current model available online, though they stress it is not ready for prime-time use. They also have worked out smartphone versions of the algorithm, but I couldn't gain access to these apps.
This study, like virtually all that hope to improve KS diagnosis, suffers from circular reasoning: it compares information collected on febrile children, but the ultimate "gold standard" of KS diagnosis depends on clinician judgment, in this case the same clinicians that are ordering tests and using the algorithm. It will be difficult to get past this hurdle in KS research until researchers learn more about etiology and pathogenesis of this condition.
I intend to "play" with this online algorithm for my suspected KS patients, and look forward to more updates/improvements from this group of investigators.
*See my September 23 posting for my insistence on using the term "syndrome" rather than "disease."
PICO Question: Among febrile children can a clinically useful algorithm differentiate Kawasaki disease from other febrile illness?
Question type: Diagnosis
Study design: Prospective cohort
Hardly a week goes by in my practice that I don't make the comment, "I hate Kawasaki Syndrome.*" I hate it because it's a very tricky diagnosis, one that ultimately we can never be certain about unless the child develops true coronary artery aneurysms. (I have my doubts about whether the finding of coronary ectasias, a subtler finding on echocardiogram, is clinically significant or unique to KS.)
So, I'm highly interested in studies aiming to improve diagnostic capabilities for KS. This study, from Stanford and UCSD, has a novel approach and is worth reading, even though the findings don't offer an immediate boost to patient care capabilities. Two tweaks to the usual diagnostic algorithm approach distinguish this study: 1) the authors utilized a sophisticated computerized system to "train" a scoring system based on clinical, laboratory, and combined data with repetitive modeling of receiver operating characteristic (ROC) curves (quick explanation: it provides a graphical view of tradeoffs between sensitivity and specificity of tests); 2) they have made their current model available online, though they stress it is not ready for prime-time use. They also have worked out smartphone versions of the algorithm, but I couldn't gain access to these apps.
This study, like virtually all that hope to improve KS diagnosis, suffers from circular reasoning: it compares information collected on febrile children, but the ultimate "gold standard" of KS diagnosis depends on clinician judgment, in this case the same clinicians that are ordering tests and using the algorithm. It will be difficult to get past this hurdle in KS research until researchers learn more about etiology and pathogenesis of this condition.
I intend to "play" with this online algorithm for my suspected KS patients, and look forward to more updates/improvements from this group of investigators.
*See my September 23 posting for my insistence on using the term "syndrome" rather than "disease."
Labels:
algorithm,
diagnostic testing,
Kawasaki disease
Sunday, April 14, 2013
Dr. Web, the New Asthma Specialist
Source: Joseph CLM, Ownby DR, Havstad SL, et al. Evaluation of a web-based asthma management intervention program for urban teenagers: reaching the hard to reach. J Adolesc Health 2013; 52:419-26; doi:10.1016/j.jadohealth.2012.07.009. See AAP Grand Rounds commentary by Dr. Nusheen Ameenuddin (subscription required).
PICO Question: Among urban African American teenagers with asthma, does a tailored, web-based asthma management program improve clinical outcomes?
Question type: Intervention
Study design: Randomized controlled
This is one of a growing number of studies suggesting that the digital world can improve health outcomes. Researchers at the Henry Ford Health System in Detroit, along with a couple other academic institutions, partnered with the Detroit public schools to study a web-based asthma management system for inner-city teens. (It's great to see academic health system/community partnership efforts!) Feedback was tailored to the individual teenager, based on responses to questions about attitudes and beliefs, targeting behaviors affected by emotional support, motivation, resistance to change, and rebelliousness. In this randomized controlled trial, improved asthma management was observed in some aspects of health outcomes in the group receiving the intervention, compared to a group receiving only generic asthma education on a different web site.
What really struck me about this study was how it was reported. In the "old days," a report of, for example, a bench research study had detailed information about the reagents, test conditions, and other study aspects, such that another investigator could accurately duplicate the experiment to verify or refute the results. In the case of this web-based study, and many others like it, the report has nowhere near the detail that would be required to independently assess the authors' findings. I did find the entry site for the web-based intervention that I'm not bothering to post here, since access is restricted and there is absolutely no detail about the content on the home page.
When comparing digital versus traditional educational programs, the biggest problem is ensuring that the actual content information is identical for both interventions. Usually, there is a significant difference in content; for example, paper-based literature has less information than web-based content, usually due to better graphics on the web site (a picture really is worth a thousand words). In the current study, we have no way of assessing differences in content, nor can we view examples of the web-based intervention which actually sounds very innovative (e.g. "radio disk jockey delivers the scientifically sound advice that is tailored to each teen"). Perhaps the investigators are hoping to copyright and sell their intervention to others, but even if that is the case I believe they could have set up a limited web site to demonstrate the differences in the group materials. Let's hope they do so in the next iteration of their innovative work.
In the meantime, practitioners should take note of this type of study. A primary care provider isn't going to have the time to develop the complex interventions utilized in this study, but (s)he can take note of the concept: even economically disadvantage teens have access to the Internet and have cell phones. Simple reminders are easy to set up and might be helpful for those with chronic disease having difficulty adhering to treatment plans. Just setting a cell phone alarm for medication reminders might make a difference. Give it a try!
PICO Question: Among urban African American teenagers with asthma, does a tailored, web-based asthma management program improve clinical outcomes?
Question type: Intervention
Study design: Randomized controlled
This is one of a growing number of studies suggesting that the digital world can improve health outcomes. Researchers at the Henry Ford Health System in Detroit, along with a couple other academic institutions, partnered with the Detroit public schools to study a web-based asthma management system for inner-city teens. (It's great to see academic health system/community partnership efforts!) Feedback was tailored to the individual teenager, based on responses to questions about attitudes and beliefs, targeting behaviors affected by emotional support, motivation, resistance to change, and rebelliousness. In this randomized controlled trial, improved asthma management was observed in some aspects of health outcomes in the group receiving the intervention, compared to a group receiving only generic asthma education on a different web site.
What really struck me about this study was how it was reported. In the "old days," a report of, for example, a bench research study had detailed information about the reagents, test conditions, and other study aspects, such that another investigator could accurately duplicate the experiment to verify or refute the results. In the case of this web-based study, and many others like it, the report has nowhere near the detail that would be required to independently assess the authors' findings. I did find the entry site for the web-based intervention that I'm not bothering to post here, since access is restricted and there is absolutely no detail about the content on the home page.
When comparing digital versus traditional educational programs, the biggest problem is ensuring that the actual content information is identical for both interventions. Usually, there is a significant difference in content; for example, paper-based literature has less information than web-based content, usually due to better graphics on the web site (a picture really is worth a thousand words). In the current study, we have no way of assessing differences in content, nor can we view examples of the web-based intervention which actually sounds very innovative (e.g. "radio disk jockey delivers the scientifically sound advice that is tailored to each teen"). Perhaps the investigators are hoping to copyright and sell their intervention to others, but even if that is the case I believe they could have set up a limited web site to demonstrate the differences in the group materials. Let's hope they do so in the next iteration of their innovative work.
In the meantime, practitioners should take note of this type of study. A primary care provider isn't going to have the time to develop the complex interventions utilized in this study, but (s)he can take note of the concept: even economically disadvantage teens have access to the Internet and have cell phones. Simple reminders are easy to set up and might be helpful for those with chronic disease having difficulty adhering to treatment plans. Just setting a cell phone alarm for medication reminders might make a difference. Give it a try!
Labels:
adolescent medicine,
asthma,
ehealth,
web-based intervention
Sunday, April 7, 2013
Clinician-Sonographers: A New Specialty?
Source: Shah VP, Tunik GM, Tsung JW. Prospective evaluation of point-of-care ultrasonography for the diagnosis of pneumonia in children and young adults. Arch Pediatr Adolesc Med. 2012;167(2):119-125; doi:10.1001/2013.jamapediatrics.107. See AAP Grand Rounds commentary by Dr. Michelle Stevenson (subscription required).
PICO
Question: Among children who undergo chest radiography in a pediatric emergency department, what is the accuracy of point-of-care ultrasound for the diagnosis of pneumonia?
Question type: Prognosis
Study design: Prospective cohort
This sounds like a great setup for a clash between our modern-day Luddites and the 21st century advance of technology in medicine. The former group would bemoan the loss of physician skills in performing a physical examination, while the latter would advise us to use whatever technology helps the patient. I agree with both views. If I pay attention, every day I see clinicians, both young and old, auscultating the chest through a child's hospital gown or shirt. If you want to detect crackles accurately, or pick up a pericardial friction rub, you'll miss it with that approach. Beyond that, how many clinicians now perform clinical maneuvers such as egophony and percussion of the chest? Last time I checked, we still teach this in medical school; we should quit sending mixed messages. (See studies by Metlay and by Gadomski for detailed analysis of accuracy of clinical evaluation for pneumonia.) On the other hand, if use of point-of-care chest sonography for pneumonia results in better patient care, I'm all for it. Which brings us to the current article. "Clinician-sonographers" (pediatric emergency medicine docs trained in chest sonography) at Children's Hospital at Montefiore and Bellevue Hospital Center in New York performed chest sonography on 200 children they suspected of having pneumonia after clinical exam. All children had a chest radiograph as well, but the clinician-sonographers did not see those results until after they had interpreted the sonograms. Eighteen percent of the children had pneumonia on radiograph. Compared to a radiologist-interpreted radiograph, sonography had 86% sensitivity and 89% specificity (increased to 97% specificity if just looking at consolidation greater than 1 cm). These numbers were much better than those derived from just the clinical examination. In general, more experienced sonographers did better than newbies in accuracy of readings, with radiologist-interpreted sonograms as the gold standard. The study does allow us an opportunity to see how to use likelihood ratios. In that best case scenario of 86% sensitivity and 97% specificity, the likelihood ratio for a positive sonogram is 7.8, while the negative likelihood ratio is 0.1. We know in this study the overall rate of pneumonia is 18%. Thus, if a child has a positive sonogram and we apply that likelihood ratio, that child's chances of having pneumonia increases to about 60%. If the sonogram is negative, the chances decrease to about 2%. Of course, most of those children have viral pneumonia, and it's pretty difficult to be certain which have bacterial disease and could benefit from antibiotic therapy. This study wasn't designed to assess impact on antibiotic prescribing or on patient outcomes, but certainly that should be the next step in research in this field, including more clinical and outcome data to judge potential impact of administering or withholding antibiotics. I could go on forever about different features of this study. It was certainly well-performed, but I feel the need to insert a cautionary note, especially since an editorial in the same issue of the journal presented a very strong plea for all of us to start doing chest sonograms in the ED immediately. The key to evidence-based medicine, in my opinion, is to assess how much impact a particular intervention will have on patient outcome. In the case of children with pneumonia, what we really want to know is whether the use of point-of-care sonography results in children getting better faster, or having less risk of being exposed to antibiotics, for example. While this study is a key step forward in understanding the role of chest sonography in children, it doesn't address patient outcomes. Let's not get carried away yet, while still urging our emergency medicine and radiology colleagues to press forward with more definitive studies.
PICO
Question: Among children who undergo chest radiography in a pediatric emergency department, what is the accuracy of point-of-care ultrasound for the diagnosis of pneumonia?
Question type: Prognosis
Study design: Prospective cohort
This sounds like a great setup for a clash between our modern-day Luddites and the 21st century advance of technology in medicine. The former group would bemoan the loss of physician skills in performing a physical examination, while the latter would advise us to use whatever technology helps the patient. I agree with both views. If I pay attention, every day I see clinicians, both young and old, auscultating the chest through a child's hospital gown or shirt. If you want to detect crackles accurately, or pick up a pericardial friction rub, you'll miss it with that approach. Beyond that, how many clinicians now perform clinical maneuvers such as egophony and percussion of the chest? Last time I checked, we still teach this in medical school; we should quit sending mixed messages. (See studies by Metlay and by Gadomski for detailed analysis of accuracy of clinical evaluation for pneumonia.) On the other hand, if use of point-of-care chest sonography for pneumonia results in better patient care, I'm all for it. Which brings us to the current article. "Clinician-sonographers" (pediatric emergency medicine docs trained in chest sonography) at Children's Hospital at Montefiore and Bellevue Hospital Center in New York performed chest sonography on 200 children they suspected of having pneumonia after clinical exam. All children had a chest radiograph as well, but the clinician-sonographers did not see those results until after they had interpreted the sonograms. Eighteen percent of the children had pneumonia on radiograph. Compared to a radiologist-interpreted radiograph, sonography had 86% sensitivity and 89% specificity (increased to 97% specificity if just looking at consolidation greater than 1 cm). These numbers were much better than those derived from just the clinical examination. In general, more experienced sonographers did better than newbies in accuracy of readings, with radiologist-interpreted sonograms as the gold standard. The study does allow us an opportunity to see how to use likelihood ratios. In that best case scenario of 86% sensitivity and 97% specificity, the likelihood ratio for a positive sonogram is 7.8, while the negative likelihood ratio is 0.1. We know in this study the overall rate of pneumonia is 18%. Thus, if a child has a positive sonogram and we apply that likelihood ratio, that child's chances of having pneumonia increases to about 60%. If the sonogram is negative, the chances decrease to about 2%. Of course, most of those children have viral pneumonia, and it's pretty difficult to be certain which have bacterial disease and could benefit from antibiotic therapy. This study wasn't designed to assess impact on antibiotic prescribing or on patient outcomes, but certainly that should be the next step in research in this field, including more clinical and outcome data to judge potential impact of administering or withholding antibiotics. I could go on forever about different features of this study. It was certainly well-performed, but I feel the need to insert a cautionary note, especially since an editorial in the same issue of the journal presented a very strong plea for all of us to start doing chest sonograms in the ED immediately. The key to evidence-based medicine, in my opinion, is to assess how much impact a particular intervention will have on patient outcome. In the case of children with pneumonia, what we really want to know is whether the use of point-of-care sonography results in children getting better faster, or having less risk of being exposed to antibiotics, for example. While this study is a key step forward in understanding the role of chest sonography in children, it doesn't address patient outcomes. Let's not get carried away yet, while still urging our emergency medicine and radiology colleagues to press forward with more definitive studies.
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