What are WEE Waiting for? The Quick-Wee Method for Faster Clean Catch Urine Collection

Where can I find this paper?

https://www.ncbi.nlm.nih.gov/pubmed/28389435

Please note this paper is OPEN ACCESS. You are strongly advised to read the original paper before reading any further.

What is this paper about (what is the research question)?

Does suprapubic cutaneous stimulation with cold fluid-soaked gauze (the “Quick-Wee” method) reduce the amount of time spent waiting for clean catch urine?

Summary of the Paper

Design: single centre, randomised, prospective non-blinded trial

Objective: to evaluate the efficacy of the Quick-Wee method

Outcome of interest: voiding of urine within five minutes (binary outcome)

Intervention: genital cleaning for 10 seconds with sterile water at room temperature, followed by continued rubbing of the suprapubic area in a circular pattern with gauze (soaked in cold saline) held by forceps

Reference standard: genital cleaning for 10 seconds with sterile water at room temperature (standard practice)

Participants: patients presenting to an Australian paediatric emergency department between September 2015-April 2016

Inclusions: pre-continent infants aged 1-12 months in whom clean catch urine sample was required

Exclusions: neonates (defined as <1 month of age); infants with anatomical or neurological abnormalities affecting voiding of urine or sensation; those patients with need for an immediate sample by invasive method

Results: 354 subjects were recruited of whom 344 participated in the analysis; 175 in the control group and 179 in the intervention group (5 patients were excluded from each group after randomisation, giving 170 in the control group and 174 in the intervention group).

54/174 (31%) of patients voided within five minutes in the Quick-Wee group

20/170 (12%) of patients voided within five minutes in the control group

The difference in proportions was 19% (95% confidence interval for difference 11-28%).

This gave an NNT of 4.7 to successfully catch one additional sample within five minutes (95% confidence interval 3.4-7.7).

Authors’ Conclusions:

The Quick-Wee method requires minimal resources and is a simple way to trigger faster voiding for clean catch urine from infants in the acute care setting.

On the study design

Firstly it is important to note that this was a single-centre study in which trained clinicians were identifying and recruiting potential test subjects in addition to performing the intervention. This introduces a potential for innovation or novelty bias, whereby new treatments or procedures are preferred (or possibly considered less favourably) than traditional treatments or methods. This could be exacerbated by a lack of blinding, such as in this study, although it would be practically impossible to blind subjects to the treatment they are receiving in this particular case. In an ideal world, the clinicians recruiting and randomising patients would be different from those performing the procedure, and the results would be interpreted by people blinded to the groups to which patients were randomised – but research rarely occurs under ideal circumstances (if ever).

That said, a considerable effort has been made to overcome this through blinding which was carried out in a 1:1 ratio of consecutive patients using random permuted blocks of different sizes and allocation concealment (opaque envelopes) selected sequentially.

The Quick-Wee procedure itself was well standardised; teaching was delivered through face-to-face intervention and written instruction and standardised packs were used for the initial cleaning phase. A separate pack was prepared for the Quick-Wee intervention itself.

Several secondary outcomes were considered, including successful catch of the specimen, contamination of sample, parental and clinician satisfaction with method.

A sample size calculation was performed, requiring 322 patients (161 in each group) to achieve 80% power to detect a difference in the primary outcome; based on pilot study data, the expected change in proportions was 15% with a baseline expected proportion of 21% in the control group and therefore 35% in the intervention arm (a small inconsistency in these percentages is likely due to rounding). The authors performed an intention-to-treat analysis and planned to recruit an additional 10% of subjects beyond the sample size calculation to account for anticipated attrition.

What were the results and what does this mean?

The study achieved the required sample size due in part to the forethought of including 10% more patients to account for attrition.

The 344 subjects analysed were divided into control (170 patients) and intervention (174 patients) groups and in each case successful voiding was determined if it occurred within five minutes of the initial cleaning step. The data collection section mentions paper case record forms but it is not clear whether these were standardised for the research study or the usual clinical documentation. In addition, interobserver reliability is inferred through the use of a timer but in practice there is an opportunity for bias here if the observer is not independent of the clinician carrying out the procedure (forgetting to press “start” and adding a few extra seconds, for example).

The results are certainly impressive; 54/174 patients voided within five minutes with the Quick-Wee method (31% – 95% confidence interval 24%-39%) compared with 20/170 in the control group (12% – 95% confidence interval 7%-18%). The difference in proportions was 19% with a 95% confidence interval of 11%-28% and a P value of <0.001 using the $χ$ ² test.

The use of binary data here certainly makes for simpler analysis rather than looking at specific timings for each subject; five minutes is not an unreasonable amount of time to wait for a sample but it should be recalled that there is a member of staff tied up in undertaking the Quick-Wee method for potentially the entire five minute duration – this might prove challenging in busy Emergency Departments.

The authors also looked at voiding with successful catch and found similar proportions (Quick-Wee 52/174 [30%: 95% confidence interval 23%-37%]; control 15/170 [9%: 95% confidence interval 5%-4%]). Does the Quick-Wee method make missed voids less likely? Perhaps, due to increased attention focus on the relevant anatomical area..!

The difference in rates of contamination was not statistically significant (27% in the Quick-Wee group [95% confidence interval 15%-43%], 46% in the control group [95% confidence interval 17%-77%] – this could be an area for further work in a larger sample, given high contamination rates in both groups.

Finally, the satisfaction scores of both parents and clinicians were better in the Quick-Wee group. The data is given in a slightly counter-intuitive way (the Likert scale runs from 1=very satisfied to 5=very unsatisfied) which they have called “higher rate” of satisfaction – it is worth noting that this does not correspond to a higher number! In the Quick-Wee group, median parental and clinician satisfaction was 2, while in the control group the median for both was 3.

What can we take from this paper into clinical practice?

This method appears to be reliable from this pragmatic and robust study. It is certainly appealing as a first-line technique over invasive methods such as suprapubic aspiration or catheterisation. It certainly seems worthy of adoption into clinical practice provided you can spare the staff.

More questions to ask

Would this technique work in older children, given its theoretical basis in the neonatal cutaneous voiding reflex?
Would warmer water work as reliably?
Would time be further reduced with a pre-emptive feed (or oral hydration) as in the study by Herreros et al?
Could this method also reduce contamination rates?

Probing Questions: Lung Ultrasound in Diagnosis and Management of Bronchiolitis

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Thanks to Casey Parker of Broomedocs for this guest contribution – his review is cross-posted here.

Where can I find this paper?

http://www.biomedcentral.com/1471-2431/15/63

What is this paper about (what is the research question)?

This paper aimed to correlate sonographic lung findings with clinically diagnosed bronchiolitis in infants. The authors also attempted to provide some prognostic information [the need for oxygen support] based on sonographic lung features.

Summary of the Paper

The subjects were infants admitted for clinically suspected bronchiolitis. There was also a cohort of “normal controls” used as a comparison. The children underwent a clinical scoring by the treating Paediatrician and lung ultrasound by both a radiologist and Paediatrician sonographer. The scans were all completed by two of the authors.

Design: Single-centre, observational cohort study conducted in an Italian Paediatric unit.

Objective: to evaluate the accuracy of lung ultrasonography in the diagnosis and management of bronchiolitis in infants.

Outcome of interest: correlation between clinical and sonographic lung findings in bronchiolitic infants. Can LUS findings be used to predict the need for supplemental oxygen requirements?

Participants: One hundred six infants, aged from 9 to 239 days old were enrolled.

Inclusions: clinically “suspected bronchiolitis” in infants. Unclear as to whether these were consecutive cases – only 106 over a 3 year study period.
Exclusions: radiological pneumonia, other “concomitant pathology” or the unavailability of the study sonographer.

Results: There was a high level [ ~90%] of agreement between the clinician’s severity rating and the predetermined sonographic severity scores. There was also a high level of agreement between the two sonographers scoring of the LUS findings (K = 89.6%). The lung US scoring predicted the need for oxygen supplementation with good accuracy [sensitivity: 96.6 %, specificity 98.7 % ] although there were wide confidence intervals as a result of the small numbers in this trial.

Authors’ Conclusions:

In summary, this pilot study demonstrates that the use of LUS in bronchiolitis can be considered as an extension of the clinical evaluation and could be incorporated into clinical algorithms to aid decision-making. Our promising data needs to be confirmed in larger cohort studies also involving critical patients.

On the study design

This study design is typical of many pilot ultrasound papers. Small numbers of patients in which sonography is compared to a gold-standard that may not be entirely accurate of itself. Bronchiolitis is a clinical diagnosis, with no really objective diagnostic standard. The use of just 2 experienced Paediatric sonographers in a single centre does raise questions about the external validity of the results and there is a high likelihood of bias here. The clinicians were blinded to the sonographic findings – and therefore the risk of bias here was removed. The use of “normal cohort” and the “RSV swabs” in the study design was a little confusing and doesn’t really add to the results.

What were the results and what does this mean?

The results suggest that clinically diagnosed bronchiolitis looks like…. sonographic bronchiolitis as per the defined criteria used in this paper. The protocol used did identify infants with more severe lung disease. The need for supplemental oxygen was consistent with more severe LUS changes. However, given the “standard” was clinical examination it is unclear exactly what LUS would add to the prognostication by paediatricians. The high degree of agreement between the two study sonographers is difficult to extrapolate given they are both highly skilled, ultrasound enthusiasts – a larger mix of observers would be needed to draw any conclusions about our ability to utilise LUS in small kids.

What can we take from this paper into clinical practice?

Lung ultrasound for the diagnosis and severity scoring of bronchiolitis is reasonably accurate. Does it add anything? Probably not, unless you are currently using CXR to ‘diagnose’ bronchiolitis. This paper does provide some useful descriptions of the spectrum of disease and their sonographic appearance.

I think this paper is interesting in that it describes the sonographic spectrum of a common disease of infants. The study is not really large enough, nor does it have the external validity to make it a “practice changer”. This pilot can help inform us about the appearance of bronchiolitis – and in the future this may become a more commonplace part of our clinical assessment of children – but for now I am not sure it adds to our quiver.

More questions to ask

Can ultrasound reliably differentiate bronchiolitis from important differential diagnoses in infants ? (e.g.. pneumonia, heart failure, upper airway obstruction… )
Are the sonographic findings in bronchiolitis consistent when obtained by sonographers of various experience?
Previous papers have compared LUS to conventional CXR for the diagnosis of bronchiolitis – and LUS was favourable. It would be nice to see a paper looking at children with severe disease in which clinicians often turn to CXR to “reconfirm the working diagnosis” in order to ascertain its utility at that end of the spectrum.

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Bouncing Back: Repeated ED Visits Among Children With Meningitis or Septicaemia

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Where can I find this paper?

http://www.ncbi.nlm.nih.gov/pubmed/25458981

What is this paper about (what is the research question)?

How often have children, subsequently diagnosed with meningitis or septicaemia, attended an ED and been discharged in the preceding five days?

Summary of the Paper

Design: retrospective cohort study using pan-Toronto hospital database

Objective: to ascertain the proportion of children with an ultimate diagnosis of meningitis and septicaemia who had attended an Emergency Department in the five preceding days

Outcome of interest: proportion of reattendances; ED factors in the group with preceding attendance compared with those admitted at first attendance

Participants: children (aged 30 days to 5 years) with a diagnosis of meningitis or septicaemia with linked data regarding prior attendances in the period 06/04/2005-01/03/2010.

Inclusions: children with an ultimate diagnosis of meningitis or septicaemia and a minimum inpatient stay of 4 days (or death in hospital)
Exclusions: length of stay <4 days, patients discharged within the preceding 14 days of admission with meningitis/septicaemia

Results: 521 children were admitted with a final diagnosis of meningitis/septicaemia during the study period. 125 had attended an ED in the preceding 5 days with 114 attending with apparent infection. Those with repeated visits had similar lengths of stay, critical care use and 30-day mortality.

Authors’ Conclusions:

Our study reveals that despite the imperative to provide early diagnosis and treatment to children and infants with critical infections, current practices differ markedly from this goal, with 1 in 5 children having repeated ED presentations before admission with meningitis or septicaemia.

On the study design

This was a retrospective cohort study which depended on ICD-10 reporting of diagnoses and database correlation to link admissions with meningitis or septicaemia with prior ED attendances. As with all such studies, findings are dependent on the quality of data recorded, even more so when the analysis is performed on retrospective data.

Nonetheless the study asks a valid question about how good we are at identifying serious bacterial illness the first time around.

What were the results and what does this mean?

The low prevalence of serious bacterial infection is interesting; there is no data given about the number of ED attendances for children who were not given a diagnosis of meningitis or septicaemia, so this reinforces the “needle-in-a-haystack” feeling we have in the UK. These diseases are thankfully rare but identifying them early is a clinical priority.

That 125 children reattended (after not being admitted at first attendance) does not resonate with me in the same way as they authors. I feel this rather reflects my experiences that patients who have severe illness do not always suddenly present acutely unwell but rather at a time point along a clinical trajectory, at which reliable clinical signs may or may not be present. Notably children who reattended had lower acuity scores at first presentation, which supports this.

Unfortunately much of the analysis is focused on whether attending a department with dedicated paediatric consultants made a difference. I suspect that this is association rather than causation and would be difficult to prove. In any case we would need to see the background rates of paediatric attendances to each unit to determine whether these district general hospitals were genuinely outliers. There may also be a parental tendency to reattend at a “specialist” hospital or a clinician tendency to admit more patients at a specialist hospital due to a higher acuity presenting there – the paper does not answer this question.

What can we take from this paper into clinical practice?

What this study seems to tell us is that diagnosis is tricky and that time and observation is valuable – and that we should not only make the most of opportunities to observe and review patients but that we should safety-net properly. Any child with any apparently benign illness may re-present with a deterioration in condition and we must ensure that parents feel confident in returning to us if that occurs.

More questions to ask

How on earth can we identify serious bacterial illness in children? Answers on a postcard for a Nobel prize… 🙂

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Talking Heads: S100B For Detection of Intracranial Injury in Mild Head Trauma in Children

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Where can I find this paper?

http://www.ncbi.nlm.nih.gov/pubmed/26283067

What is this paper about (what is the research question)?

Does S100B, a calcium-binding protein located in the cytoplasm and nucleus of astrocytes and Schwann cells, have a role in predicting intracranial injury (or its absence) for mild head trauma in children?

Summary of the Paper

Design: multicentre prospective cohort study

Objective: to determine the test characteristics for S100B in mild head trauma in children with determination of a cutoff to provide diagnostic utility.

Outcome of interest: diagnostic/predictive performance of S100B biomarker for intracranial injury in children with mild head trauma

Reference Standard: presence of intracranial injury (any collection of blood within the cranial vault or cerebral oedema) on CT scan

Participants: children aged <16 years presenting to one of three Swiss paediatric EDs between January 2009 and December 2011

Inclusions: patients with mild head injury (acute head trauma with confusion or LOC <30mins or amnesia or transient neurological abnormality) for whom a CT was performed and blood obtained for S100B assay.
Exclusions: children arriving >6h after head trauma, children with Down syndrome, patients with a history of seizure in the preceding 28/7

Results: 80 children were enrolled of whom 73 were included in the analysis. 20 (27.4%) had evidence of intracranial injury on CT although none required surgical intervention.

The area under the Receiver Operator Characteristic (ROC) curve for S100B was 0.73 (95% CI 0.60-0.86) which improved to 0.77 (95% CI 0.65-0.89) when under 2s were excluded.

Using a cutoff of 0.14micrograms/L gave a sensitivity of 95% (95% CI 77%-100%) for all children [100% (95% CI 81%-100%) with under 2s excluded] and specificity 34.0% (95% CI 27%-36%).

Authors’ Conclusions:

The biomarker S100B is a valuable tool to help the physician decide whether head CT is indicated for children aged <16 years with mild head trauma. Its excellent sensitivity indicates that it could be an accurate tool to “rule out” an intracranial injury.

On the study design

This was a small prospective study in which blood samples were taken from children presenting with mild head injury deemed by clinicians to require CT scan and analysed independently of the CT findings to permit calculation of test characteristics for the biomarker S100B.

The authors included patients under 16 presenting to one of three Swiss paediatric EDs with mild head injury (acute head trauma with confusion or LOC <30mins or amnesia or transient neurological abnormality) for whom a CT was requested; these subjects also had a venous blood sample for S100B level which was not available before CTs had been reported. They then determined test characteristics for S100B in the context of CT findings. The sample size was pretty small – 80 children were enrolled of whom 7 were excluded, either because they didn’t have the blood test at all, within 6h or they didn’t have the CT scan. This affects the applicability of the study.

Performing bloods on children in the ED is a tricky one; children with major trauma presentations frequently have blood tests taken but these children might not. It’s worth considering how many additional blood tests we might be performing if S100B is adopted into everyday practice.

The other interesting thing is the classification of “mild head injury”. These children were selected because they were having CT head (the reference standard for determining the presence or absence of intracranial injury) but the population does not completely correlate with those head injured children who would have a CT indicated according to the NICE head injury guidelines – which is going to affect whether we can directly extrapolate the results to our ED head injured population as there may be some children we would want to CT who would not have been included in this study.

What were the results and what does this mean?

Only 73/80 were included in the analysis, of whom 20 had an intracranial injury. No surgical interventions were required in any case so we may be missing this proportion of severely head injured patients which, combined with the inclusion of only “mild head injuries” means that we have really only looked at a slice of our PED head injury population.

The ROC curve for S100B had an AUC of 0.73 (95% CI 0.60-0.86) which improved to 0.77 (95% CI 0.65-0.89) when under 2s were excluded.

Using a cutoff of 0.14micrograms/L gave a sensitivity of 95% (95% CI 77%-100%) for all children (100% (95% CI 81%-100%) with under 2s excluded) and specificity 34.0% (95% CI 27%-36%). This looks good, but look at the width of those confidence intervals, reflective of the small sample size. If the true sensitivity is 77% that’s no good at all – so we definitely need confirmation with a bigger study and ideally wider inclusion, so we can apply the findings to all our head injured patients.

What can we take from this paper into clinical practice?

There’s definitely potential for S100B to be used as a lesser evil compared with radiation exposure on the developing brain. However the evidence (and, in all likelihood, the assays in your laboratory) isn’t there yet. Watch this space… I suspect there is more to come on S100B.

More questions to ask

How would S100B perform for all head injured children in a bigger study?
Do we need to exclude the under-2s to improve test characteristics – and what should we do with those children?
What is the level of sensitivity we will accept at the cost of specificity?

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Clinician Suspicion in Blunt Torso Trauma – Place Your Bets

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Where can I find this paper?

http://www.ncbi.nlm.nih.gov/pubmed/26302354

What is this paper about (what is the research question)?

Are clinicians better at predicting intra-abdominal injuries in children with blunt torso trauma than a derived clinical prediction rule?

Summary of the Paper

Design: Secondary analysis of some existing PECARN group data from a prospective cohort study of children with blunt torso trauma

Objective: to compare the test characteristics of clinician suspicion with a derived clinical prediction rule to identify children at very low risk of intra-abdominal injuries undergoing acute intervention

Outcome: test characteristics for clinician suspicion, measured against presence or absence of need for acute intervention for intra-abdominal injury.

Comparison: test characteristics of a derived clinical prediction rule from the same population.

Participants: 12044 patients recruited between May 2007-January 2010 and eligible to participate in the parent study (http://www.ncbi.nlm.nih.gov/pubmed/23375510) underwent secondary analysis.

Inclusions: children <18 years old with blunt torso trauma presenting to participating PECARN Emergency Departments
Exclusions: injury >24h prior to attendance; pre-existing neurological disorders affecting examination findings; pregnancy; transfer from another institution.

Results:

3016/9252 deemed low risk (<1%) for clinician suspicion had CT abdomen performed; 35 patients subsequently had acute intervention. Of the remaining patients with clinician suspicion ≥1%, 168/2667 had an acute intervention.

Negative clinician suspicion had the following test characteristics;

sensitivity 82.8% (95% CI 77.0-87.3)
specificity 78.7% (95% CI 77.9-79.4%)
NPV 99.6 (95% CI 99.5-99.7%)
LR- 0.2 (95% CI 0.2-0.3)

Low risk on the prediction rule had the following test characteristics;

sensitivity 97.0% (95% CI 93.7-98.6)
specificity 42.5% (95% CI 41.6-43.4%)
NPV 99.9 (95% CI 99.7-99.9%)
LR- 0.1 (95% CI 0.0-0.2)

Authors’ conclusions

A clinical prediction rule had a significantly higher sensitivity for identifying intra-abdominal injury undergoing acute intervention, but a lower specificity. The higher specificity of clinician suspicion did not translate into clinical practice as clinicians frequently obtained abdominal CT scans in patients they considered to be at very low risk.

On the study design

This was a secondary analysis of data collected as part of an original PECARN study on abdominal trauma in children. It’s always worth remembering that while secondary analysis can reveal some very useful information and trends, this was not the original purpose for which the study group was recruited or the study powered (although the authors tell us this study was preplanned, and the standardised data collection forms used to collect information about clinician decision making supports this).

The study has an issue in that the “gold standard” abdominal CT was not applied to all patients, only those deemed to be at risk of injury. This means there is a large portion of patients who had no imaging and no intervention who may still have had intra-abdominal injury although without a need for clinical intervention the significance of this is doubtful.

Good attempts were made to follow subjects up to ensure no clinically important outcomes were omitted.

What were the results and what does this mean?

There is an important distinction in this paper between the presence of an abdominal injury and one requiring intervention (specified as death, therapeutic intervention at laparotomy, angiographic embolisation, blood transfusion for anaemia or administration of intravenous fluids for at least two nights). This composite reference standard is pragmatic but we could argue about whether intra-abdominal injuries not requiring intervention are also clinically relevant or not, considering the comparative risks of radiation exposure with abdominal CT.

It is worth noting that not all of the 12044 subjects enrolled had CT abdomen performed. 11919 were deemed to have no suspicion of injury, which we must doubt given the fact that neither clinician suspicion nor clinical prediction rule achieved 100% sensitivity.

The study found that in patients with intra-abdominal injury requiring intervention, the clinician correctly identified the risk as ≥1% in 82.8% (95% CI 77.0-87.3) of cases, and in patients who did not have intra-abdominal injury requiring intervention, the clinician correctly identified that the risk was <1% in 78.7% (95% CI 77.9-79.4%) of cases. Unfortunately this shows that clinician judgement alone is neither sensitive nor specific enough to support decision making in isolation. This is borne out in a high CT abdomen rate in the population, despite a high proportion of low risk patients.

The decision rule, which determined risk as “not low” in the presence of any one of:

no evidence of abdominal wall trauma or seat belt sign
GCS >13
no abdominal tenderness
no evidence of thoracic wall trauma
no complaints of abdominal pain
no decreased breath sounds
no history of vomiting after the injury

had better sensitivity (so the absence of these signs performs better as a predictor of the lack of need for CT and intervention) but poorer specificity (i.e. the presence of any sign does not accurately predict a need for intervention).

Of note there were three patients whose injuries were not identified by clinician prediction or derived clinical prediction rule, so neither predictor achieved 100% sensitivity.

What can we take from this paper into clinical practice?

We as clinicians rely a lot on clinical judgement but that alone is a poor predictor of the need for intervention for intra-abdominal injury, especially when compared with this non-validated derived prediction rule. Following validation the prediction rule may have some diagnostic utility, especially when combined with observation.

More questions to ask

How will this decision rule perform when validated?
How would the rule perform if the specificity of clinician judgement was incorporated?

Oxygen Saturation Targets in Bronchiolitis – Magic Numbers?

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Where can I find this paper?

http://www.ncbi.nlm.nih.gov/pubmed/26382998 – this paper is currently open access

What is this paper about (what is the research question)?

Is a target oxygen saturation of 90% or higher equivalent to 94% or higher for resolution of illness in acute viral bronchiolitis?

Summary of the Paper

Design: multicentre, parallel group, randomised controlled equivalence trial with allocation concealment.

Objective: to determine whether accepting a reduced lower limit target oxygen saturation in infants with viral bronchiolitis affected time to resolution of illness

Primary outcome measure: time to resolution of cough (parental reporting)

Intervention: subjects were randomised following decision to admit, to either standard SpO2 monitoring or a modified oximeter which skewed the reading such that SpO2 90% read as 94%. All other care was standard.

Participants: 615 subjects randomised between 03/10/2011-30/03/2012 and 01/10/2012-29/03/2013. 308 randomised to standard group, 307 to modified oximeter group

Inclusions: infants aged 6 weeks to 12 months (corrected gestational age) with clinically diagnosed bronchiolitis admitted to hospital for supportive care following presentation to the Emergency Department or Acute Assessment Area
Exclusions: preterm (<37 weeks) who had received oxygen in past 4 weeks; cyanotic or haemodynamically significant heart disease; CF or interstitial lung disease; documented immunodeficiency; direct admission to HDU/ICU; previously randomised

Results: Median time to cough resolution was 15.0 days in both groups with a median difference of 1.0 days (95% CI -1 to 2). This fell between the prespecified equivalence limits of plus and minus two days.

Authors’ conclusions

In children with acute viral bronchiolitis, the time taken for symptoms to resolve was the same whether they were managed to a target oxygen saturation of 90% or 94%.

On the study design

This study used eight centres to recruit a sample with 80% power to detect non-equivalence of greater than two days in time to resolution of cough. Cough resolution was determined by parents at pre-determined follow-up phonecalls (7, 14, 28 days and 6 months). Some allowances were made for inaccurate recording of this data using random selection of a date between the last time the cough was known to be present and the first date it was noted to be absent (if available). This method of reporting does still leave the outcome open to some parental bias and accuracy of reporting cannot be guaranteed.

Allocation to a group was concealed until definite enrolment, and the allocation was masked to study staff, hospital staff and parents. It’s not clear why the authors have chosen to use the work “masking” rather than “blinding”.

Several interesting secondary outcomes were also recorded although it is always worth remembering that studies are designed and powered to detect differences in the primary outcome and may be underpowered to detect differences in secondary outcome. The authors decided in advance to statistically analyse time until “fit for discharge” and actual discharge date for both groups, along with parental anxiety scores and whether the child was fit to attend daycare.

What were the results and what does this mean?

Following some loss to follow-up and protocol violations, 293 subjects were analysed in the standard group at 6 months and 291 in the modified oximeter group. This still reflects a study population greater than that determined by the power calculation. There was no difference in the median time to cough resolution which was 15.0 days in both groups.

The authors addressed both intention to treat analysis (analysing those subjects with protocol violations – being given the wrong oximeter probe – according to their original allocated group) and per-protocol analysis (analysing them only if they fulfilled the allocation from start to finish) and found this did not affect the results.

The modified group also had quicker return to adequate feeding and “back to normal” time. Patients in the modified group, predictably, received supplemental oxygen in fewer cases, for a shorter period, were considered fit for discharge sooner and were discharged sooner. There were fewer serious adverse events and adverse events in the modified group (35 SAEs in 32 infants in the standard group vs 25 SAEs in 24 infants in the modified group). The modified group had increased HDU admissions (13 episodes in the modified group vs 8 in the standard group) but fewer reattendances (26 in the standard group vs 12 in the modified group).

The authors postulate that having a higher target oxygen saturation influences decisions about fitness for discharge and that the increased use of oxygen in the standard group might have adversely affected feeding through drying of nasal passages, reflected in the time to adequate feeding. They also suggest that increased time in hospital in the standard group might expose these infants to nosocomial infection, causing the increased readmission rate – but of course this is all speculation 🙂

What can we take from this paper into clinical practice?

It seems that infants subjectively recover from bronchiolitis at the same rate even if we target SpO2 90% or above instead of 94% or above. However this was a population for whom a need for admission to hospital had already been identified and the extrapolation of this to the Emergency Department population is not wholly appropriate. We can be reasonably relaxed about SpO2 90-94% in these patients but until further work is done to reflect our undifferentiated population we should probably be careful about assuming we can safely discharge these infants.

More questions to ask

Would we see the same resolution and patterns of return to normal behaviour/complications in the undifferentiated ED population of infants with bronchiolitis?

15th May: Should We Cool Children Following Out-Of-Hospital Cardiac Arrest?

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Where can I find this paper?

http://www.ncbi.nlm.nih.gov/pubmed/25913022

What is this paper about (what is the research question)?

Does therapeutic hypothermia increase the proportion of patients surviving at one year with good functional status following paediatric out-of-hospital cardiac arrest?

Summary of the Paper

Design: single-blinded, multicentre randomised controlled trial

Objective: to determine whether therapeutic hypothermia after out-of-hospital cardiac arrest confers a benefit in children

Primary outcome measure: survival at 12 months with good neurological function (defined as age-corrected standard score of 70 or more on the Vineland Adaptive Behaviour Scales (VABS-II)

Intervention: subjects were randomly assigned in 1:1 (permuted blocks stratified by age) to therapeutic hypothermia (target temperature 33°C) for 48h then normothermia (target temperature 36.8°C) for 72h, or normothermia for 120h. Active cooling was undertaken in either case to achieve the target temperature.

Participants: 295 patients randomised between September 2009 – December 2012. 155 were randomised to hypothermia, 140 to normothermia.

Inclusions: patients aged 48hrs-18 years presenting following out-of-hospital cardiac arrest to one of 38 sites in the US and Canada, having required chest compressions for at least two minutes and with an ongoing requirement for mechanical ventilation after return of spontaneous circulation (ROSC)
Exclusions: inability to undergo randomisation within 6h, score of 5-6 on the motor component of the Glasgow Coma Scale, decision to withhold aggressive treatment, major trauma as cause of arrest, patients with pre-existing VABS-II score <70

Results:

Survivors at 12 months with VABS-II score >70

Hypothermia 27/138 (20%)

Normothermia 15/122 (12%)

Risk difference 7.3 (95% confidence interval -1.5 to 16.1)

Relative likelihood 1.54 (95% confidence interval 0.86 to 2.76, P=0.14)

Authors’ conclusions

In comatose children who survive out-of-hospital cardiac arrest, therapeutic hypothermia, as compared with therapeutic normothermia, did not confer a significant benefit with respect to survival with good functional outcome at one year.

On the study design

The study was utilised multicentre collaboration to recruit a sample with 85% power to detect a 15-20% difference in the primary outcome between treatment groups. This was a pragmatic design; although the subjects and those providing care to the patients could not be blinded to the intervention, reasonable steps were taken to ensure that the investigators recording the primary outcome were a) independent from those delivering care and b) blinded to the arm of the study to which subjects had been randomised.

Unlike other studies, the normothermia in this case was also an active decision; the patients’ temperature was actively controlled according to the group to which they were randomised.

The authors tells us that other than the temperature targeted, care between the groups was identical although they later state that “all other aspects of care were determined by the clinical teams.” This does leave us to wonder what if and how knowledge of the treatment arm and expectation of its efficacy (or otherwise) might have influenced those treating clinicians.

What were the results and what does this mean?

There was no statistical difference in survival with a good neurological outcome at 12 months between the two groups. In the secondary outcomes, there was no difference in absolute survival between the groups, nor in the reduction in neurological performance score, however there was increased incidence of hypokalaemia and thrombocytopenia in the hypothermia group and increased requirement for renal replacement therapy in the normothermia group.

Results were analysed using intention to treat analysis, which includes subjects in the final analysis of the arm to which they were randomised irrespective of whether they dropped out of the study or received an alternative treatment in the end. This is a conservative approach which can help to ameliorate the effects of unpleasant side effects of treatments; there’s a nice explanation of intention to treat here. It helps give us a realistic expectation of the results we might see in clinical practice.

What can we take from this paper into clinical practice?

In this study the null hypothesis was no difference between the groups, this study doesn’t prove that hypothermia is harmful or not beneficial; there is simply insufficient evidence to reject the null hypothesis of no difference, based on this study. We should continue to follow local protocols in terms of cooling but this paper does give clinicians a little additional confidence in deviating from protocols if indicated.

More questions to ask

Is there evidence for cooling patients following in-hospital cardiac arrest?
Would a larger sample size demonstrate a benefit and is this feasible?

Reducing PED Reattendance Rates

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Where can I find this paper?

http://www.ncbi.nlm.nih.gov/pubmed/25162691

What is this paper about (what is the research question)?

Can we reduce the number of reattendances to the paediatric emergency department by telephoning within 24h of discharge?

Summary of the Paper

Design: Single-centre, prospective randomised controlled trial

Objective: to examine whether a follow-up telephone call by a non-health care provider from the ED within 24h of discharge can reduce the rate of returning to the ED within 72h

Outcomes: rate of return visits within 72h of discharge. It is unclear how this was determined but subjects were contacted by telephone at 96h after discharge in both intervention and control groups.

Intervention: follow-up phone call within 12-24h of discharge undertaken by a “research assistant” (medical student)

Comparison: standard care (i.e. no follow up phone call)

Participants: convenience sample of parents of patients presenting to a single centre between 1st July 2009 and 30th August 2009.

Inclusions: parents of patients for whom the responsible clinician thought ED discharge was likely
Exclusions: families without a telephone, those who left without being seen, those leaving against medical advice

Results: 371 subjects were recruited of whom 171 were in the study group and received a follow-up phone call and 200 were in the control group. Demographics were broadly similar between the two groups.

24/171 in the study group reattended within 72h (14%)

14/200 in the control group reattended within 72h (7%)

There was a statistically significant difference between reattendance rates with a greater proportion of reattendances in the intervention group (p<0.03).

Authors’ conclusions

Emergency Departments practicing follow-up calls without response to medical questions should consider a forecasted increase in return rates

On the study design

This is a single centre pseudo-randomised controlled trial – the authors tell us that it was pseudo-randomised because there were research staff available to recruit at different hours of the day. It’s not clear exactly how this statement refers to randomisation but if the time of day patients presented to the ED predicted whether they entered the intervention or control group then there’s potentially a major confounder in the first premise of the paper.

Inclusion and exclusion criteria seem reasonable but the demographics of the subjects throws up some interesting issues; the mean age of the presenting child was 5.7years with a mean parental age of 38.3 years. I can’t help but wonder whether a similar study in my own department would reveal a rather different (substantially younger) parental population and there are sociological implications to this.

There is no sample size calculation so although there were reasonable numbers in each group we don’t know whether the study was fundamentally underpowered and unable to detect a statistical difference between groups. Whether this statistical difference represents a clinically relevant outcome measure is also in question (and addressed below).

What were the results and what does this mean?

On the surface it seems that telephone follow-up within 12-24 hours of ED discharge increases rather than decreases reattendance rates, but the picture is rather more complicated.

Firstly, there is an intrinsic uncertainty surrounding the value of follow-up calls by non-healthcare professionals. Of particular note, the telephone interviews were undertaken by medical students. It seems that conversations were one-way; parents were asked whether they had any questions but there was no opportunity for them to be answered. It seems possible that introducing the concept that there might be unanswered questions could actualise occult parental anxiety, prompting them to seek clarification from a healthcare professional.

Secondly, it’s not even clear how reattendance data was obtained. Was this self-reported by parents at the 96h phone call? It seems so – in which case it could almost certainly have been collected more reliably using ED computerised records.

Thirdly, all manner of data about these reattending subjects is omitted. Were they actually unwell and then admitted to the hospital? Were all reattenders in both groups discharged from ED again? Without this information it is difficult to ascertain whether reattendance was inappropriate.

What can we take from this paper into clinical practice?

Follow-up phone calls by non-healthcare professionals do not seem to reduce reattendances. However it’s unlikely that this model would ever be rolled out and there are plenty of other questions we still need answers to.

More questions to ask

Are these effects the same in an adequately powered study where outcomes are divided into admission or discharge at reattendance (arguably more clinical relevant)?
Would attendances be reduced if phone calls were made by healthcare professionals and provided an opportunity to obtain advice and have questions answered?

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19th July – Does Bedside US Measurement of the IVC Diameter Correlate with CVP in the Assessment of Intravascular Volume in Children?

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Where can I find this paper?

http://www.ncbi.nlm.nih.gov/pubmed/23426248

What is this paper about (what is the research question)?

Can we use bedside ultrasound measurement of IVC diameter as a proxy for fluid status (as determined by CVP measurement) in children?

Summary of the Paper

Design: prospective observational study

Objective: to compare bedside US assessment of volume status with CVP measurement in critically ill paediatric patients

Outcomes: correlation of US assessment of volume depletion with CVP assessment

Test of interest: beside US measurement of IVC diameter and calculation of IVC/aorta ratio, defining dehydration as “collapsability index of 50% or greater and an IVC/Ao ratio of 0.8 or less.” Diameter measured in subxiphoid sagittal and subxiphoid transverse views.

Reference Standard: invasive CVP measurement by digital transduction at distal port of previously sited CVC

Participants: convenience sample of patients aged <21y admitted to the Paediatric Critical Care Unit (Intensive Care) at a single centre between July 2010 and June 2011

Inclusions: patients requiring invasive haemodynamic monitoring
Exclusions: patients in whom US measurement of IVC could not be performed due to technical limitations

Results:

72 eligible patients of whom 51 enrolled to the study. Sagittal view was obtained in 100%, transverse view in 84% of subjects.

Correlation of collapsibility index and CVP: -0.23 (P=0.11)

Correlation of IVC/Ao ratio and CVP: -0.19 (P=0.22)

Authors’ conclusions

We did not find a correlation between the 1-point measurement of either the collapsibility index or the IVC/Ao ratio and CVP measurements in critically ill paediatric patients.

On the study design

This paper is an interesting one; the use of ultrasound to determine the need for and response to fluid resuscitation is controversial in adult patients, so it is not surprising to see that the uncertainty about clinical usefulness translates to paediatric practice. In addition, assessment of hydration/dehydration in children is notoriously difficult and the search for objective measures which reflect clinical endpoints is clearly relevant.

This paper is an observational study which means that there was no change made to the patient’s care in response to the measured data. The population may or may not reflect our ED patients; by definition, patients already admitted to PICU (at least in the UK) have usually a) been unwell for some time and b) had some level of resuscitation – so it is difficult to know how their volume status might be affected by preceding use of fluid boluses (particularly if hypertonic solutions were used). That said, the vast majority of critically ill paediatric patients in the ED do not have central access amenable to CVP monitoring and there are obvious issues with designing a study which necessitates insertion of CVCs which might not be necessary (unethical) or are going to be inserted in the ED (impractical – numbers likely to be very small). The fact that the recruitment was a convenience sample also reflects the otherwise small numbers and unpredictable nature of critical illness in children and while a more robust sampling method would be preferable, convenience sampling is often seen in studies where a single investigator has a particular skill set necessary for the collection of study data.

A bigger problem is the use of CVP as a marker of haemodynamic status; although it is frequently measured in the ICU and PICU, it is notoriously poor at reflecting volume status as a single measure and demonstrating clinically relevant response to fluid bolus when measured continuously, as raised in this review paper from 2008. So the study is comparing a questionable method of determining fluid status with one which is equally questionable – not exactly a great starting point. Perhaps a longer term outcome – such as fluid balance over the subsequent 24-48h, urine output, need for fluid boluses – might have given a clearer and more reliable picture.

There was also little consistency between the patients; CVC measurement occurred at a variety of anatomical sites and there was no correction or account taken for other variables which might affect CVC readings (such as abdominal surgery or positive pressure ventilation).

What were the results and what does this mean?

This is a great opportunity to revise correlation!

There’s a great wikipedia article on Spearman’s rank correlation coefficient here, but essentially correlation measures the level of interdependence between two non-parametric variables. It tells us whether as one variable increases, the other increases, and the strength of this relationship.

In the paper, both correlation co-efficients quoted in the results section were negative, suggesting that as CVP increases the IVC variable (IVC/Ao ratio or collapsibility index) decreases, and vice versa. The small numbers (-0.11 and -0.23) imply a near random relationship (remember, the nearer the correlation coefficient is to zero the less related the two variables appear to be; the nearer to 1 or -1, the stronger the relationship and the more predictive one variable is of the other). The performance characteristics (sensitivity, specificity, NPV and PPV) for both US-calculated variables were poor.

However, there are very small numbers here; of the 52 children included, only 21 actually had a CVP <8mmHg (the cutoff used by the authors to determine intravascular volume depletion). In any study where such a small number of patient have the target condition we have to wonder whether different patterns might be seen in a larger sample – the probability of a type II error is high.

What can we take from this paper into clinical practice?

So, assessment of paediatric intravascular volume status remains a mystery for now. Previously published studies have suggested that IVC/Ao ratio is lower in children who are otherwise clinically assessed as being dehydrated and that the value rises following fluid boluses, but we cannot be sure from this current paper that US measurement reflects CVP. Should we use ultrasound to assess intravascular status? This paper finds it a poor proxy for CVP – which again is a poor proxy for volume status. So on the basis of this study – no, but there is clearly more work to be done here.

More questions to ask

Do serial IVC measurements reflect response to fluid bolus in a clinically meaningful way?
Would we see better correlation using a single CVC line site, or excluding “less central” central lines such as femoral CVC?
Should we be aggressively fluid-resuscitating children anyway?! – see this interesting FOAM paper on new insights from the FEAST trial

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5th July 2013: Comparison of cosmetic outcomes of absorbable versus nonabsorbable sutures in pediatric facial lacerations

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Where can I find this paper?

http://www.ncbi.nlm.nih.gov/pubmed/23714755

What is this paper about (what is the research question)?

Do non-absorbable and absorbable sutures give comparable cosmetic results for repair of simple facial wounds in kids?

Summary of the Paper

Design: multicentre, randomised controlled, single blinded trial with allocation concealment

Objective: to compare long-term cosmetic outcomes of absorbable versus non-absorbable sutures based on physician scoring of facial lacerations in the paediatric population

Outcomes: primary – visual analogue scale assessment of wound acceptability made by physicians, blinded to suture material, at 3 months. Secondary – caregiver completion of same visual analogue scale plus completion of satisfaction questionnaire

Intervention: closure of wound by standard approach using 5.0 fast-absorbing surgical gut (FAC) without removal of sutures

Reference Standard: closure of wound by standard approach using 5.0 non-absorbable suture (NYL) with removal of sutures at 4-7 days

Participants: patients presenting to two urban paediatric EDs in Philadelphia April 2008-April 2010

Inclusion – English speaking patients aged 1-18 years with isolated, non-contaminated linear facial wounds between 1-5cm in length assessed by clinicians as requiring closure by suture

Exclusion – irregular or contaminated wounds/bites, wounds>8h old, patients with complex wounds, immunodeficiency, bleeding/clotting disorder, pregnancy, diabetes, renal dysfunction, or allergy to local anaesthetic

Results: 98 patients were recruited of whom 49 had closure with FAC and 49 with NYL. 85 were followed-up at 4-7 days (42 FAC,43 NYL) and 76 at 3months in person or by telephone (FAC 37, NYL 39). Telephone follow up did not include VAS score.

61 patients had completed VAS scores at 3/12 (FAC 29, NYL 32)

Mean VAS scores by physicians:

FAC 57.6, NYL 67.6

Difference in means -10 (95% CI for difference in means -19.6 to -0.4)

Authors’ conclusions

We are not yet able to conclude that absorbable sutures are equivalent to nonabsorbable sutures with respect to cosmetic outcomes of facial lacerations in children.

On the study design

There is little information on how patients were recruited, but other than the restriction of English-speaking patients inclusion and exclusion criteria seem sensible.

The allocation concealment and blinding is helpful in reducing bias, but I would question whether leaving absorbable sutures until completely absorbed is standard practice – it isn’t mine, and therefore this impacts the external validity of the study.

The plan for follow-up at 3/12 seems sensible and is rationalised by the authors but this seems early to fully assess the “long-term” impact of wound closure.

While the exact suture material does not necessarily replicate standard UK practice it is reasonable to assume little difference between non-absorbable and absorbable suture material around the globe.

What were the results and what does this mean?

The trial is a non-inferiority trial – the aim is to show that using absorbable suture material does not give a perceptibly inferior cosmetic result. The visual analogue scoring undertaken by blinded physicians (and averaged between three scorers) showed not only lower VAS satisfaction scores for the absorbable suture group but a 95% confidence interval which did not cross zero, suggesting the study was unable to demonstrate non-inferiority. The validity of the VAS has been assessed elsewhere but there is a considerable difference between physician and caregiver scores.

It is also important to remember that despite sample size calculations which predicted attrition of 40%, only 61/98 recruited patients actually completed the full study protocol and had photographs for assessment by VAS – so the study was insufficiently powered.

What can we take from this paper into clinical practice?

It appears that if we use absorbable sutures and don’t remove them, there are noticable differences in wound healing at 3/12; there’s insufficient evidence in this paper to convince us that not removing sutures provides a comparable cosmetic result in the first three months.

More questions to ask

Are there benefits to using absorbable sutures and then removing them (in the same timeframe as we would normally remove non-absorbable sutures)?
Would we see non-inferiority at a later review – 18 months after closure perhaps?
Would we see non-inferiority in an appropriately powered study?

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