This month, The Lancet – Respiratory Medicine published a randomised controlled trial investigating whether patients with sepsis could benefit from antibiotics administered by EMS crews.
I think the results were not quite what people would have expected! In #PHJC style, we are going to have a go at critically appraising the paper. As always, don’t take my word for it, go and have a read of the paper and make your own conclusions.
I don’t pretend to be an expert on sepsis or antibiotics, but I’m OK at critically appraising papers, so if you’d like more of a commentary on the paper, I can direct you to this interesting editorial:
This was the first prehospital randomised controlled trial comparing prehospital administration of antibiotics to septic patients against standard care. The study reports that patients in the intervention arm of the study received antibiotics quicker, but did not demonstrate a benefit to all-cause mortality at 28 days. The authors conclude that prehospital antibiotics for patients with sepsis is not recommended.
The nitty gritty
Did the study ask a clearly focussed question?
The population studied
Patients with sepsis, severe sepsis or septic shock.
Inclusion criteria were >18 years of age; a diagnosed or suspected infection; a temperature > 38 or less than 36 and at least one other criterion of the systemic inflammatory response syndrome (heart rate >90bpm or respiratory rate >20 per min, or both). Sepsis severity was grouped in to uncomplicated sepsis, severe sepsis, and septic shock, using the 2001 SSCM/ESICM/ACCP/ATS/ International Sepsis Definitions Conference guidelines. As the Sepsis-3 criteria came out in 2016, the investigators did a subgroup analysis after retrospectively putting patients in to categories according to qSOFA criteria.
Exclusion criteria were allergy to ceftriaxone or other beta-lactam antibiotics, known pregnancy, or suspected prosthetic join infections.
I think this is where one of the major limitations of the study comes in. The inclusion criteria allows for patients who may not necessarily have sepsis, but perhaps suffering an infection with no associated organ dysfunction. Nearly 40% in both the intervention and control group had non-severe sepsis. This broad inclusion criteria meant that patients who may not have necessarily benefited from early antibiotic treatment were included in the study. This may also be why the study reported mortality rates of 8%, whereas previous studies that looking at patients with severe sepsis and septic shock have reported in-hospital mortality rates 26 – 30%. Only 3% in the intervention group and 2% of the usual care group were considered to have septic shock.
The investigators did a subgroup analysis, analysing just those patients with severe sepsis and septic shock and again found no benefit in receiving prehospital administered antibiotics. However, the numbers were very small and this would not have been adequately powered.
The intervention given
ceftriaxone 2000mg intraveneously & usual care (fluid resuscitation and supplementary oxygen)
The comparator given
Worth noting that before the study, all participating EMS nurses received training to recognise sepsis and the local guidelines were modified. A comprehensive set of protocols for detecting and treating sepsis were added to the participating ambulance regions.
The primary outcome considered
all-cause mortality at 28 days.
What type of study was it?
This was a nationwide randomised controlled open label trial. If we look at our good friend, the hierarchy of evidence, we see that RCTs are the ‘gold standard’ study design for evaluating the effects of interventions.
Was the assignment of patients to treatments randomised?
Patients were randomised with a 1:1 ratio to which treatment group they were allocated to using block randomisation with blocks of size 4 and stratified per region.
Oh, ok. What does that mean?
Well, patients are randomised to either receive antibiotics or standard care in order to achieve an equal distribution of baseline characteristics in each group to reduce the chance of confounding effecting the results. Block randomisation with blocks of size 4 means that for every 4 patients enrolled in to the study, 2 would receive antibiotics (A) and 2 would receive standard care (B). The order in which the 4 are allocated is random. It could be AABB, ABAB, ABBA, BBAA, BABA, BAAB. Doing this helps ensure that there is a similar number of participants in each group. If simple random allocation was used, it would be possible to get many more patients in one group than the other (e.g. in a group of 100 you could get 80 assigned to intervention and 20 assigned to control, due to the nature of randomness).
As this was a mutlicentre study with 10 EMS services participating, for each service patients were recruited in groups of 4 and allocated a treatment using the block randomisation. This is in effect stratifying the participants by region. This minimises confounding between treatment groups in those characteristics that might vary between EMS regions across the Netherlands.
However, when we read this paper we see that despite the 1:1 ratio and block randomisation there is quite a large difference in numbers of participants in the intervention (1150) and control group (1548). The authors state that this is due to the over enthusiastic study EMS nurses wanting to treat more patients with antibiotics and therefore opening envelopes until they found one that randomised patients to the antibiotic group. This is called allocation bias, when there is a difference in the way patients are allocated a treatment. Randomisation would have prevented this if the protocol was adhered to, but as the study personnel deviated from this, because they felt certain patients would benefit from antibiotics even though they weren’t randomised in to that group, the study is susceptible to allocation bias. The authors do note that despite this, the baseline characteristics were still similar between the groups.
Were the patients, workers and study personnel ‘blind’ to treatment?
Another way this allocation bias could have been prevented is if the study used a double-blinded design, rather than being open label. An open label study is when the researchers and patients are aware of who was in which treatment group, there is no ‘blinding’ or ‘masking’. This means the study could have been open to ‘ascertainment bias’, which is where there is a distortion of the outcome measures by the investigators, as they know which participants where in which group. This can also be called assessor bias. Ascertainment bias can also result if the patient reports exaggerated effects, say if they disappointed at not receiving a treatment, they may report feeling not as well. This is called response bias. As the primary outcome used in this study is objective (dead or not at 28 days), this would reduce the chance of ascertainment bias influencing the results of the primary outcome.
Having a double-blind study, where the intervention could have been compared against a placebo, would have reduced the possibility of allocation bias, as everyone would have been receiving either a placebo or antibiotics, but no one would know who was receiving which. However, I think this wouldn’t be feasible, as the hospital staff would need to know whether they needed to give the patient antibiotics or not when they arrived at the hospital (as my brother kindly pointed out to me when I asked him to proof-read this blog).
Were all of the patients who entered the trial properly accounted for at its conclusion?
Eighteen patients that were randomised to groups were lost to follow up and eight withdrew consent.
Once randomised, always analysed.
The study used an Intention To Treat (ITT) design and analysis. This means that every patient is analysed in the group they were randomised to, regardless of whether they actually received the treatment or not, were lost to follow-up or didn’t comply with the protocol. As the old adage goes ‘once randomised, always analysed’. The authors report that treatment violations occurred in 40 patients in the usual care group (who were given antibiotics), and 12 in the intervention group (who did not receive antibiotics). In an ITT analysis, these patients would still be analysed in the groups they were randomised to. ITT analysis means that the groups remain comparable, due to the randomisation to intervention or control groups, and also gives a more accurate reflection of what would happen in clinical practice, as for instance, sometimes patients don’t always take their medication or tolerate an intervention well. The CONSORT guidelines recommend ITT analysis as standard analysis for RCTs. In order to do a ITT analysis, complete data of the outcomes are needed, otherwise some complex statistical methods such as imputation are needed.
If an analysis was done where only the patients who complied with the protocol/not lost to follow up etc were included, and those that didn’t were excluded, this would be called a per protocol (PP) analysis.
Were the groups similar at the start of the trial?
Table 1 shows that baseline characteristics for both groups were similar at the start of the trial.
Aside from the experimental intervention, were the groups treated equally?
The authors don’t report on any big differences. The only thing I can notice is that more patients in the intervention group received IV fluids (64% vs 34%).
How large was the treatment effect?
The study reports no statistically significant differences between patients who received prehospital antibiotics and those that received usual care, in terms of 28-day all cause mortality (antibiotics 8% vs usual care 8%, RR 0.95, 95% CI 0.74 – 1.24). Note the small difference in RR and a confidence interval that crosses 1.
There were also no statistically significant differences in regards to 90 day mortality, ICU admission or median length of stay in ICU or hospital. Patients who received usual care had higher 28-day readmission rates (usual care 10% vs antibiotics 7%, p = 0.0004)
There was quite a difference in terms of the times to receiving antibiotics between the two groups. The median Time To Antibiotics (TTA) before arriving at the emergency department for patients in the intervention group was an impressive 26 min (IQR 19–34). TTA after arriving at the emergency department in the usual care group was 70 min (IQR 36–128). For patients in the usual care group, a longer TTA was not associated with an increase in 28 day mortality (p=0·23).
So it’s interesting that despite receiving antibiotics much sooner if they were administered in the ambulance, this didn’t seem to make a difference to 28-day mortality.
Cant the results be applied in your context?
This study was undertaken among EMS services, so we don’t have the challenge of deciding whether the results can be generalised to the prehospital setting, as we do with some hospital based studies. The study was set in the Netherlands, with 10 large EMS services and 34 hospitals as participating sites. Having a multi-centre study like this increases the generalisability (external validity) of the results. However, the EMS services in the Netherlands are not necessarily identical to the EMS services in the UK. In the Netherlands EMS nurses work in ambulances, so a different set of professionals with different training providing the prehospital care, to what we have in the UK.
Are the benefits worth the harms and costs?
While there are some limitations to this study, it is the best quality of evidence available addressing the question of whether patients with sepsis would benefit from receiving antibiotics in the ambulance. The results demonstrate no benefit.
What about the harms? Jean-Louis Vincent, who authored the editorial on this paper, writes about the concern of using ceftriaxone on all infected patients, in a time when efforts to prevent antimicrobial resistance (AMR) are so high.
What are the authors conclusions? Do you agree?
The authors of the study conclude that:
…we currently do not advise antibiotic administration in the ambulance to patients with suspected sepsis
Do I agree with the authors conclusion? Based on this study, I would say yes. It would have been good if the inclusion criteria was more refined to only include patients that would be most benefited from the treatment, and I hope such a study will be done in the future. However, at the moment this is the best available evidence we have on this topic.