Category Archives: Critical Appraisal

Critical Appraisal of a Paper

14th December 2012: Ibuprofen & Codeine for Pain Management in Children

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Where can I find this paper?

http://www.jem-journal.com/article/S0736-4679(12)01136-5/abstract

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

Is codeine in combination with ibuprofen better at improving paediatric pain scores for children presenting to the ED with limb injuries than ibuprofen alone?

Summary of the Paper

Design: single centre, randomised, double-blinded placebo-controlled trial

Objective: to compare the efficacy of a combination of codeine with ibuprofen to codeine alone for the management of pain in children with limb injuries presenting to the ED.

Computer generated block randomisation with double blinding was used.

Intervention: 1mg/kg codeine syrup plus 10mg/kg ibuprofen caplet

Comparison: placebo syrup plus 10mg/kg ibuprofen caplet

Primary outcome: difference in mean pain score between initial score at triage (T1) and 90mins after administration of medication (T3). Validated visual analogue scale (VAS) was used for pain scoring.

Population: children aged 7-18 years presenting to a tertiary paediatric ED between Feb 2008-Nov 2009, between 10am-4pm, with musculoskeletal limb injury in preceding 72h

  • Inclusion: pain score >3 on 0-10 VAS at triage, French/English speaking, limb with bony tenderness, swelling, limited range-of-movement or angulation <30deg.
  • Exclusion: allergy to opioids, NSAIDs or food colouring, critical illness, injury requiring orthopaedic reduction, trauma to >1 limb, social/physical abuse, cognitive deficit, chronic pain, analgesia in last 6h

Results: 83 patients enrolled from 279 eligible patients, 81 analysed; 40 in experimental and 41 in control arms. 47% had presented with fractures

Mean pain score at T1: experimental 5.9 +/- 1.7, control 5.7 +/- 1.3

Mean pain score at T3: experimental 4.0 +/- 2.4, control 4.1 +/- 2.0

Mean difference in pain scores between T1 & T3: -0.1 (95% CI -1.3 to 1.0), p=0.55

Authors’ Conclusions:

The addition of codeine to ibuprofen did not significantly improve pain management of children with a musculoskeletal trauma. Pain control provided by the medications remained suboptimal for most patients.

On the study design

Despite being a convenience sample, there are plenty of good methodological examples to be found in this paper. The use of allocation concealment (randomisation by computer generated blocks) and placebo, and careful preservation of blinding until after completion of the study are good examples of the role of study designers in reducing human influence on the results. The paper gives details as to how randomisation was carried out, which increases our faith in the strength of the methodology.

Arguably, a convenience sample reduces our ability to apply this data to our general PED population, however it could be countered that the majority of paediatric injury presentations occur between 09:00 and 21:00. In my clinical experience, the weighting does fall towards the evening, so perhaps an adjustment of the research nurse’s hours to reflect this might have been sensible.

There are a great number of inclusion and exclusion criteria, but these seem straightforward and sensible. The key to measuring the outcome (pain) is an ability to understand and communicate a pain score as per VAS, and many of the criteria are designed around ensuring that outcomes can be measured accurately in the sample. After all, for severely injured children we are likely to consider stronger opioids/opiates (such as diamorphine or fentanyl via the intranasal route), so if there is an analgesic role for codeine in PED it is likely to be in those children with mild-moderate pain.

It is worth noting that children requiring plaster immobilisation had to wait until the full 2hr study period had elapsed before their plaster was applied. I can understand that  this might cause a confounding effect, but I wonder if further studies might help us to quantify the benefit of splintage? Anecdotally from working with adults, plastering a fractured limb does provide relief. With increasing use of ultrasound to identify fractures at the bedside, should our emphasis be towards plastering earlier in the clinical encounter (and perhaps x-ray after plaster instead of before)?

What were the results and what does this mean?

The sample size calculation undertaken prior to the study required 28 children to be analysed in each arm at T3 in order to achieve power to detect a difference in means of 1.5. We can see this was achieved (31 patients remained in each arm at T3).

There was no statistically significant difference in mean pain scores between the two treatment arms at T3, which suggests no benefit in adding codeine to ibuprofen for these patients. Of note, one patient in the experimental arm complained of nausea. It would seem sensible to consider an alternative analgesic for co-administration.

What can we take from this paper into clinical practice?

Codeine is infrequently suggested for paediatric analgesia in my experience. As discussed above, if there is a role for its use it would likely be in those patients with mild-moderate pain. This is not supported by the findings of this study and as such it seems unlikely that anyone will be advocating the use of codeine for paediatric pain as yet.

More questions to ask

  • How can we best provide analgesia for children with limb injuries?
  • Does the role of robust splintage (e.g. plaster) compare favourably with analgesic agents?

Follow us on twitter: @PEMLit

7th December 2012: Validating the Difficult Intravenous Access Clinical Prediction Rule

 

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Lots of discussion about this already on Twitter – let’s take a look!071212

Where can I find this paper?

http://www.ncbi.nlm.nih.gov/pubmed/23187988

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

How good is the Difficult Intravenous Access (DIVA) clinical prediction rule at identifying paediatric patients likely to require more than one attempt at intravenous cannulation.

Summary of the Paper

Design: prospective cohort study

Objective: validation of the DIVA score with derivation of test characteristics.

Test of interest: DIVA, a 4-part weighted clinical prediction rule. A score of 4 or more was thought to predict patients “50% more likely than the mean success rate to have a failed IV placement on the first attempt”

Success was placement of an intravenous cannula through which saline could be flushed without compromising the vein.

Primary outcome: test characteristics

Population: children aged 0-14 years requiring IV placement presenting to the ED of Mayo General Hospital in Ireland

  • Inclusion: children requiring IV placement
  • Exclusion: children requiring emergency treatment

Results: 500 children were recruited, 133 were younger than one year.

Mean failure rate was 22% – the authors state that 110 had a failed IV placement on first attempt (this doesn’t quite add up – see below).

151/500 had a DIVA score ≥ 4, of whom 57 (37.7%) had a failed IV placement on first attempt.

349/500 had a DIVA score <4, of whom 55 (15.8%) had a failed IV placement on first attempt.

For cutoff ≥4: sensitivity was 75.9%, specificity 51.8%, PPV 84.4%, NPV 37.7%.

Authors’ Conclusions:

This study validated the DIVA CPR in a population similar to that originally studied. Its acceptability and usefulness needs to be further accessed by health professionals involved in IV placement.

On the study design

The great thing about this study is that it appears highly generalisable – at least on the surface. All children who required IV access were eligible for inclusion between ages 0-14years and they were only excluded if IV was required as an emergency. The circumstances seem to reflect standard ED practice; topical local anaesthetic was used (although we don’t know which one) and doctors were limited in their attempts at cannulation before seeking help.

There are a few methodological issues though. Although we know a good amount about the population from which the sample was obtained, we don’t know how it was obtained – was it consecutive in a time frame? What time frame? Was it a convenience sample? Were these children selected at random? These factors might all affect the results – and we need to know them.

There are also some ethical issues – while there was a clear policy for seeking help after three failed attempts, it is unclear whether a second doctor was any more experienced/skilled at cannulation than the first. It would be nice to think that a senior doctor’s assistance was being enlisted. The study does have ethical  approval, but I wonder  whether this reflects standard rather than ideal practice.

We don’t know which local  anaesthetic was used; was there consistency here? Again, this might confound the results, or affect their external validity.

What were the results and what does this mean?

So, the results don’t add up, which is the first problem. Even if we take the authors’ word for the sums being right, the test characteristics are pretty useless. It’s easy to imagine that a ROC curve would have a pretty small area under the curve.

We also don’t have confidence intervals for the test characteristics. These are vital for gaining a true feeling for the usefulness of the data. There’s a great youtube resource explaining the importance of confidence intervals here.

What can we take from this paper into clinical practice?

Lots of questions! Much of the conversation on twitter asked whether this was even a relevant clinical question; @damian_roland wondered whether those who didn’t recognise the challenge of cannulation in infants – especially ex-prems – should be attempting cannulation.

There were also questions about what we should do with children for whom DIVA predicts difficult cannulation. Should we forego all cannulation attempts? Should we go straight for IO access? As much as I advocate timely IO as an approach for anyone with difficult access, the numbers don’t seem good enough to draw that sort of conclusion – but we do need to understand what we would want to  do with the findings before investing much more time in further validation of the rule.

What’s interesting is that in the paper children for whom failure was absolute went on to have enteral  rehydration by the NG route. There  is a cultural hesitancy around NG but it could certainly be argued that where it is possible it is  more physiological than intravenous hydration – so shouldn’t we be trying this before repeated IV attempts instead of afterwards? It also raises the question – who is deciding that these children need IV access? Is that also coming  from  doctors with one month of paediatric experience?

Lastly, we can reflect on the sites used for cannulation with greatest success. In my experience,  local anaesthetic is often applied by nursing staff to the antecubital fossa, particularly in the ED, whereas my preference is the dorsum of the hand. In the paper, the back of  the hand was used in 78.7% of successful cannulations. It would be interesting to  look at relationships between success  and site, considering where local anaesthetic  had been placed and whether doctor preference was expressed in advance of this.

More questions to ask

  • What do we want to use this data for in a clinical  context?
  • Has this paper simply highlighted a need to consider NG route for rehydration before IV?

Read the Twitter conversation here

Follow us on twitter: @PEMLit

30th November 2012: Diagnostic Value of Procalcitonin in Well-Appearing Young Febrile Infants

 

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Where can I find this paper?

http://www.ncbi.nlm.nih.gov/pubmed/23109682

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

How good is procalcitonin at predicting the presence of serious bacterial infection in children – and in particular, those aged ≤ 3months of age?

Summary of the Paper

Design: Retrospective multicentre diagnostic trial.

Objective: to assess the value of procalcitonin in diagnosing serious bacterial illness and in particular invasive bacterial infections in well-appearing infants with “Fever Without Source” (known as pyrexia of unknown origin in the UK)

Reference standard: serious bacterial infection, defined as isolation of pathogen from blood, CSF, urine or stool, or invasive bacterial infection – isolation of bacterial pathogen from blood or CSF.

Test of interest: procalcitonin measured using quantitative immunochemiluminesence assay.

Population: Retrospective inclusion of cases from 5 Spanish and 2 Italian PEDs

  • Inclusion: infants ❤ months of age with fever of unknown origin for whom procalcitonin was measured and blood culture performed.
  • Exclusion: patients in whom source of fever could be identified, patients classed as appearing unwell at presentation, patients who were afebrile without thermometer confirmation of fever prior to attendance, patients in whom procalcitonin was not measured, not recorded or blood culture not obtained.

Results: 1531 infants ❤ months of age with fever of unknown origin identified over 3 year period (exact recruitment period variable by centre) across three centres. 1112 included for analysis.

26% were diagnosed with serious bacterial infection, 2.1% with invasive bacterial infection.

Multivariate logistic regression analysis was performed for risk factor variables. Only PCT ≥ 0.5ng/mL was an independent risk factor for invasive bacterial infection: OR 21.69 (95% CI 7.93-59.28), with an area under the curve for SBI 0.739 (95% CI 0.702-0.776) and for IBI 0.825 (95% CI 0.698-0.952).

Authors’ Conclusions:

Among young infants with fever without source, procalcitonin is a better marker than CRP for identifying patients with invasive bacterial infection and also seems to be the best marker for ruling out invasive bacterial infection.

On the study design

We have discussed previously the issues of retrospective design. There are issues here about the inclusion and exclusion criteria; many are reliant on subjective variables such as “appearing well”. Arguably this has inherent reliability problems and we could argue the accuracy of physician assessment is dependent on exposure to paediatric patients and experience levels.

Inclusion of patients for whom both procalcitonin and blood culture were performed seems to instinctively select out a population for whom there are red flag signs (or symptoms) of underlying illness, even though the subjects were considered to appear “well” and no source of fever was apparent on examination.

The issue of reference standard is important too. We know that some children are undoubtably septic but no organism is definitively cultured, despite best efforts. Absence of diagnostic culture does not equate to absence of serious or invasive bacterial infection.

What were the results and what does this mean?

The results here are a little complicated, so bear with me.

It’s difficult to even produce a 2×2 table; the raw data doesn’t seem to be there. Procalcitonin <0.5ng/mL has a negative LR of 0.66 (95% CI 0.59-0.73) which implies that the odds of a patient with a procalcitonin level <0.5ng/mL having underlying serious bacterial illness is 0.66 times the odds that the patient with a procalcitonin above this level has underlying serious bacterial illness. The LR of a negative procalcitonin (<0.5ng/mL) for invasive bacterial illness is even more compelling: 0.25 (95% CI 0.12-0.55).

As we have seen on other papers, the confidence intervals are quite wide.

As for the predictive power of a raised procalcitonin, where the level was ≥2.0ng/mL the LR was 7.12 for serious bacterial illness (95% CI 4.52-11.21) and 11.14 for invasive bacterial illness (95% CI 7.81-15.89). So the odds that a patient with a raised procalcitonin has underlying serious bacterial illness is 7.12 times the odds that a patient with a raised calcitonin doesn’t have serious bacterial illness, and for invasive bacterial illness the odds of disease presence are 11.14 times the odds that there is no disease when the procalcitonin is ≥2.0ng/mL

What can we take from this paper into clinical practice?

Procalcitonin seems to be a useful indicator that underlying bacterial illness might be present (≥2.0ng/mL) or absent (<0.5ng/mL).

Looking at the area under the ROC curves, it doesn’t appear that procalcitonin is quite good enough to definitively rule in or out the presence of underlying bacterial illness. The retrospective design and tight inclusion criteria also limit the extrapolation of these results to the undifferentiated PED population.

More questions to ask

  • How useful would procalcitonin be when tested prospectively in an undifferentiated PED population – including those who appear “sick”?
  • What do we clinically do with patients whose procalcitonin falls between these two cutoff points?
  • How would the results be affected by a standardised investigative approach to infants with febrile illness without clear source?

Follow us on twitter: @PEMLit

23rd November 2012: Early Lactate Testing in Undifferentiated Paediatric SIRS

Where can I find this paper?

http://www.ncbi.nlm.nih.gov/pubmed/23167859

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

Does an ED measurement of hyperlactataemia (serum lactate ≥ 4.0mmol/L) predict increased risk of organ dysfunction within 24h?

Summary of the Paper

Design: single-centre prospective observational cohort study

Objective: to ascertain whether an ED serum lactate of ≥4.0mmol/L predicts risk of organ dysfunction within 24h in paediatric patients presenting with systemic inflammatory response syndrome (SIRS)

Intervention: point-of-care venous lactate measurement

Primary outcome: organ dysfunction within 24h of triage time, classified following International Paediatric Sepsis Consensus Conference definitions.

Population: convenience sample of patients presenting to ED of tertiary children’s hospital over 1 year (recruitment occurring 17/24h per day)

  • Inclusion: patients <19 years old with temperature >38.5 or <36 and HR>2 standard deviations above normal for age, undergoing phlebotomy or CVC access as part of their care
  • Exclusion: patients transferred from other institutions, patients with known inborn errors of metabolism, lactate not measured within 15mins of IV therapy initiation.

Results: 239 eligible subjects enrolled (missed eligible rate 36%), of whom 8% were admitted to an intensive care unit.

Mean lactate was 2.0 (+/- 1.2) mmol/L. 8% of subjects had hyperlactataemia. 5% of subjects had organ dysfunction within 24h; 4% of the low lactate population, 22% of the hyperlactataemic population.

Hyperlactataemia had an LR+ of 5.0 (95% CI 1.9-13.0) for organ dysfunction within 24h, sensitivity 31% (95% CI 13-58%), specificity 94% (95% CI 90-96%).

The relative risk of lactate ≥ 4.0mmol/L was 5.5 for 24-hr organ dysfunction

Authors’ Conclusions:

Serum lactate measurement identifies a population at higher risk for severe outcomes than the broader Paediatric ED population with fever and tachycardia and would be a useful addition to clinical assessment in paediatric sepsis clinical and research protocols.

On the study design

As with so many papers, the convenience sampling presents a potential problem in extrapolating this data to our own EDs. While convenience sampling is common, practical and understandable, it does impact the external validity.

To their credit, the authors have been honest about this, giving us a “missed inclusion” rate of 36%. This suggests that greater than 1/3 paediatric patients presenting with two SIRS criteria do so in 29% of the 24h period. We can only imagine how including these patients would affect the results.

The inclusion criteria are interesting too; I would suspect that many more than 239 patients present to an average PED with fever and tachycardia in 12/12 (particularly as we know that the annual attendance is around 80,000). This means that a large number of these patients did NOT have blood tests. This, of course, represents our standard practice (we don’t bleed every child with a temp and tachycardia), but it means we can only really consider the value of lactate measurement in those children whom we already deem to be systemically unwell. It would also be useful to know if a capillary lactate could help to identify those patients for whom we are not sure whether blood tests are necessary.

What were the results and what does this mean?

Despite small numbers, the study was adequately powered by their own calculation. The relative risk of lactate ≥4.0mmol/L for 24-hr organ dysfunction means that patients with an initial lactate above 4.0mmol/L have 5.5 times the risk of 24-hr organ dysfunction as those with a lactate below 4.0mmol/L. They also had 2.2 times the risk of serious bacterial infection, 4.6 times the risk of positive culture and 4.4 times the risk of ICU admission.

The low sensitivity sensitivity (31% (95% CI 13-58%)) tells us that we cannot be reassured by an initial normal lactate (we are unable to use it to “rule out” serious illness), but the specificity is  reasonable at 94% (95% CI 90-96%) – raised lactate should raise our concern. Clinically, a high specificity is more useful to us as arguably it is more important to reliably rule-in serious illness.

What can we take from this paper into clinical practice?

If we are taking bloods in children in the ED because they have signs of SIRS, a venous lactate may help with risk stratification by predicting those more likely to require antibiotics and organ support. It is probably worth taking one if you are taking bloods, but a normal lactate is not reassuring. It is not yet clear how this applies to children about whom we are unsure as to the need for blood tests.

More questions to ask

  • How would the results differ if we obtained a venous (or capillary) lactate from  all paediatric patients meeting the two SIRS criteria used in this paper (temperature and heart rate)?
  • How would results be affected  if we included children recruited around the clock rather than a convenience sample?

Follow us on twitter: @PEMLit

21st November 2012: Accuracy of Point-of-Care US for Diagnosis of Elbow Fractures in Children

**Sincere apologies for the delay in this post (due 16th Nov, delayed by technical problems)**

Where can I find this paper?

http://www.ncbi.nlm.nih.gov/pubmed/23142008

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

How good is ultrasound at diagnosing elbow fractures in children?

Summary of the Paper

Design: prospective, observational, multi-centre diagnostic study

Objective: to determine the performance characteristics of ED ultrasound by PEM physicians for diagnosis of elbow fractures in children

Test under evaluation: ED (point-of-care) ultrasound of the elbow (scanning protocol pre-determined) to determine presence of lipohaemarthrosis OR elevated posterior fat pad

Reference standard: plain radiographs reported by radiologists blinded to ultrasound findings. Clinical follow-up with notes review or structured telephone follow-up; radiologist report used if follow-up imaging performed.

Primary outcome: determination of test characteristics

Population: convenience sample of patients aged up to 21yrs presenting to either of two urban EDs when a trained study physician was available, between Sept 2010 and Dec 2011.

  • Inclusion: possible elbow fracture requiring radiographic assessment
  • Exclusion: elbow radiographs already obtained, previous confirmed elbow fracture, open wound at the elbow, unstable vital signs, severe life threatening injuries requiring resuscitation.

Results: 130 patients enrolled, fracture present on initial ED radiography in 38/130. 5 additional fractures diagnosed on follow-up radiography (23 patients).

Elevated posterior fat pad was seen on initial XR in 57/130 patients (44%): 36 with fracture, 21 without (of whom, 4 patients had fracture identified on follow-up).

Elevated posterior fat pad OR lipohaemarthrosis was seen on ED US in 68/130 patients.

Elevated posterior fat pad OR lipohaemarthrosis gave the following test characteristics: sensitivity 98% (95% CI 88-100%), specificity 70% (95% CI 60-79%), PPV 0.62 (95% CI 0.50-0.72), NPV 0.98 (95% CI 0.91-1.0), LR+ 3.3 (95% CI 2.4-4.5), LR- 0.03 (95% CI 0.01-0.23)

Authors’ Conclusions:

With focused musculoskeletal ultrasonographic training, novice PEM sonologists were able to attain the skills necessary to perform point-of-care elbow ultrasonography to evaluate for fracture by assessing the posterior fat pad for elevation and lipohaemarthrosis. 

On the study design

Despite including “children” up to the age of 21 (!), there are many positive points about the methodology in this paper. The authors involved two centres over 16 months and although the sample was obtained as a convenience sample, the wide inclusion and few exclusions mean that there’s a good chance that the population is representative of patients seen in my ED.

There are reasonable attempts to minimise bias:

  • Standardised training
  • Blinding of radiologists to US results/clinical findings
  • Standardised data collection sheet for clinical/examination findings
  • Composite reference standard (telephone follow-up)

In addition, it seems pragmatic – with only 1hr training plus 5 practice scans PEM clinicians could achieve an agreement of 0.94 with an experienced PEM sonologist! What concerns me slightly is how unclear it is who these PEM clinicians were. We can all think of the colleagues who would jump at the chance to take part in a study like this; the fact that only one sonologist had prior experience of elbow ultrasound does NOT mean that the others were inexperienced with US in general. Would these results be reproducible in the hands of a not-quite-sure-which-end-of-the-probe-goes-where EM clinician – even with an hour of training? I’m not so sure…

However, the study is nicely designed and would be relatively easy to replicate in your own department.

What were the results and what does this mean?

For diagnostic studies, it can be helpful to draw a 2×2 table. This allows the calculation of test characteristics. Below is a 2×2 table for the presence of posterior fat pad OR lipohaemarthrosis on elbow US.

    REFERENCE STANDARD
    Positive Negative Total
US Positive 42 26 68
Negative 1 61 62
Total 43 87 130

Sensitivity of 98% is not terrible, although the 95% confidence interval (88-100%) is pretty wide. This means the “true” sensitivity of elbow US in ED could be as low as 88%. Remember, high sensitivity means that when the test is negative we can effectively rule out the disease (fracture). Would we be happy to rule out at 88%? I don’t think so.

What’s most interesting is that the LR+ for elevated posterior fat pad AND lipohaemarthrosis is 5.8; that is, the proportion of patients who have a fracture and these findings is 5.8 times the proportion of patients with these findings who do not have a fracture. We can surmise that finding both elevated PFP and LH would be highly suggestive of an underlying fracture; but would this prevent an x-ray? Unlikely (pesky orthopods)! We don’t know quite how this correlates with the degree of required intervention (were these the fractures which needed to go to theatre; that were horrible looking supracondylar fractures from the outset?). And the LR- is not particularly brilliant when we look at the confidence intervals.

Not all patients who were followed-up had repeat XRs, but this reflects clinical practice and I think it is pretty reasonable not to XR a child who is pain-free with normal range of movement at their follow-up appointment. In fact, the radiation would be hard to justify. It is worth noting that four patients could not be followed-up; all had negative US and negative XR at their initial visit and were included in the “no fracture” group. The authors made reasonable attempts to follow-up these patients; how would the results be altered if we assumed the worst for these cases? And does it matter?

What can we take from this paper into clinical practice?

With appropriate training and practice, EM clinicians could use ultrasound to reliably exclude elbow fractures in children. However, a larger study is needed to tighten those confidence intervals; further training might also have this effect.

If both lipohaemarthrosis and elevated posterior fat pad are identified on US it is very likely that there is an underlying fracture, but would this change clinical practice? Probably not – yet 🙂

More questions to ask

  • Would more training/greater patient numbers narrow the confidence intervals (so we can effectively rule-out elbow fracture with ultrasound)?
  • Would the results be reproducible with a joe-bloggs ED clinician who’s a bit wobbly with an US probe (like me)?
  • Could we ever persuade orthopods to manage patients on the basis of US-diagnosed fractures without corresponding radiographs?

Follow us on twitter: @PEMLit

9th November 2012: Improving Asthma Control with Medication Review in PED

Where can I find this paper?

http://www.ncbi.nlm.nih.gov/pubmed/23111345

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

Can we improve the quality of life of paediatric asthmatic patients using the opportunity to increase their medications offered when they present to the ED?

Summary of the Paper

Design: Prospective cohort study

Objective: To assess the impact of improving control medications on quality of life in children with persistent asthma symptoms attending the PED.

Intervention: initiation or improvement of long term control medication – inhaled corticosteroid –  at discharge from PED following presentation with persistent asthma symptoms (in accordance with national guidelines).

Primary outcome: improvement in “Quality of Life”, defined as validated symptoms and quality of life scores (PACT and ARQoL), ascertained by parental reporting at telephone follow-up at 2 weeks, 6 weeks and 6 months after PED discharge.

Population: Patients presenting to PED of tertiary hospital in Bilbao (Spain) between May-December 2010 with persisent asthma symptoms

  • Inclusion: Children aged 1-14 years attending with acute asthma and persistent asthma symptoms with or without control medication
  • Exclusion: Children with chronic cardiopulmonary and neuromuscular conditions, children <1 year old, children <2 years old presenting with first episode of wheeze, children whose asthma control medication had been modified in preceding 4 weeks.

Results: 1954 asthma episodes of which 164 had persistent symptoms. 146 were included in the study with 22 lost to follow-up. At presentation, 50 (40.3%) were receiving maintenance treatment.

Asthma control medication was initiated in 74 patients (59.7%), improved within the same “step” in 36 (29.0%) and “stepped up” in 14 (11.3%).

Average PACT categorisation at 6 weeks was significantly lower than at 2 weeks (median 12, IQR 13.3 versus median 7.8 IQR 10, p<0.001) with improvement sustained at 6 months.

Mean ARQoL scores at 6 weeks and 6 months were significantly higher than those at 2 weeks (91.9 +/- 11.0 and 93.0 +/- 10.0 versus 86.1 +/- 14.3, p<0.001)

Authors’ Conclusions:

Where long term asthma control medications were initiated or stepped up following PED visit, children showed a decrease in persistent symptoms and improvement in quality of life.

On the study design

The lack of control group in this paper is a major downfall; children were presenting with intercurrent illness, a major confounder. We know from practice that asthma exacerbations are often associated with viral infection, and that wheeze and cough can persist for a few weeks afterwards. It is not surprising, then, that children were better 6 weeks and 6 months after attendance than at 2 weeks. How meaningful are these outcomes? It might be more useful to match patients with controls and demonstrate improvement, ideally through less subjective variables (time off school, hospital reattendance).

There is a risk of inclusion bias considering the seasonal recruitment.

The other issue is with data processing; subjective scores are qualitative or ordinal data at best. The study design seems to convert this to quantitative non-normal data for analysis. There is also significant confusion between averages: the authors state that “the mean PACT categorization was significantly lower”, then provide data for a median. These descriptive variables are suitable for different types of data; what kind of data did the authors have? I am no statistician but it does make me wonder whether they knew what they were doing – and whether we can trust their results and analysis.

What were the results and what does this mean?

It appears that the patients in the study had better quality of life and fewer asthma symptoms at 6 weeks and 6 months than at 2 weeks after PED discharge. However, the validity of this data is uncertain and even if the apparent improvement is reflected in real life, the lack of control group means we cannot attribute it to the introduction or adjustment of asthma medication.

What can we take from this paper into clinical practice?

Unfortunately, very little more than the idea that there might be a role for reviewing asthma medications in PED, in conjunction with a primary care physician.

More questions to ask

  • If we introduce a control group for comparison, does the adjustment or introduction of control medication improve quality of life/asthma symptoms?
  • Does this translate into objective outcomes such as reduced annual ED attendances/reduced school time missed?

Follow us on twitter: @PEMLit

Videolaryngoscopy Vs Direct Laryngoscopy

2nd November 2012: Videolaryngoscopy Versus Direct Laryngoscopy in Simulated Paediatric Intubation

Where can I find this paper?

http://www.ncbi.nlm.nih.gov/pubmed/23083969

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

In the setting of simulated paediatric intubation, is use of a videolaryngoscope associated with higher “success” rates than traditional direct laryngoscopy?

Summary of the Paper

Design: Prospective case-control study (subjects acting as own controls)

Objective: To compare the effect of videolaryngoscopy performed by trained Emergency Physicians on outcomes related to intubation.

Control: Direct laryngoscopy performed using videolaryngoscope with video display off (equivalent to laryngoscopy with Miller 0, Miller 1 or Mac 3 blade for neonate, infant and adult respectively)

Exposure: Videolaryngoscopy performed using Storz videolaryngoscope, with participants directed to watch the screen rather than looking into the oropharynx.

Intervention: Attempted intubation of three mannequins (neonate, infant and adult) in randomised order with or without presence of “pharyngeal swelling ” (determined by coin toss).

Primary outcome: “Successful” intubation, defined as successful placement of an endotracheal tube in the trachea of the simulation mannequin before removal of the laryngoscopy blade. The outcome was determined by unblinded post-attempt review of 3-point video footage by study investigators.

Population: Fellows and faculty in Paediatric Emergency Medicine volunteering to participate at a single tertiary care paediatric hospital (Philadelphia, USA).

  • Inclusion: Physicians with “adequate” training and experience with intubation
  • Exclusion: Fellows in their first year who had not completed requisite airway management training in the operating room

Results: 26 subjects performed 156 intubations Data was available for 148 intubations.

  • First attempt success in newborn: DL 20/24 (83%), VL 22/24 (92%). Difference 9% (95% CI: -9 to 28%)
  • First attempt success in infant: DL 21/24 (88%), VL 17/24 (71%). Difference -17% (95% CI: -38% to 5%)
  • First attempt success in adult: DL 10/26 (39%), VL 21/26 (81%). Difference 43% (95% CI: 18 to 67%, p=0.002)

First attempt success was significantly worse with VL than DL when pharyngeal swelling was turned on.

Authors’ Conclusions:

Paediatric emergency medicine providers had improved first-attempt success at intubation using videolaryngoscopy with a curved blade in an adult simulator; success rates with straight blades in neonatal and infant simulators were not significantly different between direct laryngoscopy and videolaryngoscopy.

On the study design

This was a small scale prospective study generating paired data. The subjects acted as their own “controls”, comparing normal DL technique with VL. There is considerable potential for selection bias in this study; subjects volunteered to participate. We can all imagine those of our colleagues most likely to volunteer to participate in this sort of study (and those who wouldn’t), and how this might skew or influence outcomes.

The scenario order was randomised, which increases the stringency of the methodology, but the lack of blinding of the investigators assessing the primary outcome is unfortunate as this might introduce an observation bias.

The introduction of the “pharyngeal swelling” component is an interesting one; the rationale for randomly including this complicating factor is unclear. While this might better represent “real life” clinical situations it does introduce a potential confounding factor for which the authors do not completely account. This might have been better placed in a separate study.

What were the results and what does this mean?

We can see from table 1 that there was a difference in time since last adult intubation between the “fellows” and the “attending physicians” which seems more significant than the for the other age groups, although there is no p-value given for this.

The investigators looked at comparative proportions of success between groups. The confidence intervals were wide but crossed zero in both the neonatal and infant mannequins, implying no evidence of significant difference in success rates. A bigger study would be expected to tighten these confidence intervals.

For the adult mannequin, the 95% confidence interval was similarly wide but did not cross zero. This suggests that the probability of observing a demonstrable difference in success rate between the groups if in fact there is no difference (the null hypothesis is true) is 0.2% (or 1 in 500). However the width of the confidence interval suggests that the “true” magnitude of the difference between the two observed groups could be between 18% and 67%.

What can we take from this paper into clinical practice?

Not much yet! The paper suggests that the use of a videolaryngoscope in the simulation setting does not significantly reduce intubation success in neonate and infant mannequins, and may improve performance in adult mannequins when used by skilled PED clinicians.

However, the controlled environment of the simulation room and the anatomy of the mannequin may well impact the realism of the situation, and the study is a proxy for clinical intubation success at best. More research is needed as the true value of videolaryngoscopy is still unclear.

More questions to ask

  • How does the use of videolaryngoscopy translate into clinical ED practice, particularly in a pressured environment?
  • Are these results reflected in physicians with less intubation experience?
  • Would training/experience with the videolaryngoscope improve performance further?

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