This one comes to us from the Children’s National Medical Center in Washington DC and is particularly heartbreaking: a 2-year old with congenital heart disease suffering a post-surgical Pseudomonas aeruginosa infection. Pseudomonas infections are particularly liable to become resistant over the course of antibiotic treatment, and in this case treatment options were limited by allergic reactions to several drugs.
With the help of scientists at Fort Detrick, a bespoke phage therapy was implemented. A two-phage cocktail known to be active against the patient’s isolate was identified, formulated and administered to the patient on two occasions.
Although phage therapy did not save the child, the authors claim that the phage therapy sterilized his bacteremia. The evidence for this claim is that several negative blood cultures followed phage administration and that phage therapy “coincided with clinical improvement” with no further details.
The whole of the evidence for efficacy is contained in this chart, which plots out time to positivity of blood cultures during the course of treatment:
Time to positivity of blood cultures is not a very reliable metric of anything. It is loosely correlated with initial amount of bacteria, but can be affected by any number of other factors, such as antibiotic and neutrophil levels present in the blood sample. Since there’s no real trend of any kind in their chart, you should disregard the y-axis and just consider the data to be a series of pluses and minuses.
The claim of bacteremia sterilization is then based entirely on the observation that phage therapy was given, and negative blood cultures were obtained subsequently – 5 days after the first round of treatment, and immediately after the second round.
The case that this is not just a random coincidence is strengthened by the observation that prior to PT, 16 consecutive positives had been returned. If we take the simplest form of the null hypothesis, that PT had no effect and that the overall frequency of positives (28/36 = 0.78) was unchanged, then this is a fairly strong argument. The probability of observing 16 consecutive positives by chance alone when the overall frequency is 0.78 is only 0.7816 = 0.02. Another way to look at it is to note that the pre-PT culture positivity was 16/16 (100%) and post-PT was 12/20 (60%) and ask if this difference is significant via a contingency table analysis:
So that’s an argument in favor of the efficacy of PT, but it is not nearly as strong as it appears. As with most faulty statistical arguments, the problem is not calculation but underlying premises. In this case, the questionable assumption is that nothing other than PT changed the probability of getting a positive blood culture. That is almost certainly not true.
The paper gives no details on blood culture, and I doubt the doctors have any clue as to how it was performed. But what you should know is that the sensitivity of blood culture, particularly for children, and more particularly for hypotensive children, is not so great.
Standard protocols for adult blood cultures call for 30 mL of blood to be drawn in 3 bottles in order to achieve a sensitivity of >90%. The reason why so much blood is needed is that even very sick patients have very low concentrations of bacteria in their blood: the average positive culture has a starting concentration of ≤1 CFU/mL. Although children are thought to typically have much higher levels of bacteria, most still have <10CFU/mL. Getting a positive signal from such low numbers of bacteria is inherently difficult and apt to fail.
There’s no way, of course, that you can draw 30mL of blood routinely from a 2-year old. 1-5 mL is more typical, but even this level can be problematic once a patient goes septic and blood pressure drops. The chance that the sensitivity of blood culture remained the same throughout the course of the case study as the child sickened and died is roughly zero. Any statistical argument that incorporates this assumption is misleading.
If you’ve read my previous takes on PT studies (here and here) you won’t be surprised that I think the phage doses given were far too low to plausibly have an effect. This study is especially egregious with regard to dosing. I argued that a dose of 109 phage in the Acinetobacter case was much too low; the current study dosed at 105 phage per dose – 4 logs lower.
I’m sorry, but it’s just not physically possible to achieve efficient attack on target bacteria at a phage concentration of 100 PFU/mL (assuming a volume of distribution of 1L). This is 5-7 logs lower than the concentrations routinely used in lab studies, where phage infection appears instantaneous.
Using a typical observed rate of phage infection of host bacteria of 10-9mL/min, the observed rate of infection by phage would be 102 x 10-9 = 10-7 (one in 10 million) per minute, a rate that is functionally indistinguishable from zero. The diffusion of large macromolecular assemblies like viruses is painfully slow, a fact that seems unknown to many phage biologists, not to mention clinicians.
Those calculations are for well-mixed suspensions, of course. If the infection focus was in a spot where phage accumulate (like the liver), it is conceivable that a few phage could have successfully infected a few bacteria, which would have then released new phage at a high local concentration that then went on to make a serious dent in the infection.
It’s possible, but is clearly a special pleading, unbacked by any evidence whatsoever.
This is a hard case, and I’m glad the boy’s physicians gave phage therapy a try. But it pisses me off that they did such a poor job of it, giving it almost no chance to work. I don’t really blame the doctors – they can’t be expected to know anything about the kinetics of phage infection. But there really is no excuse for the scientists growing the phage at Fort Detrick not to know this. Their innumeracy meant that this child had almost no chance of benefitting from PT. That’s not acceptable.