Cells that vomit fungus and other issues of science papers

This weeks journal club was on Cryptococcus neoformans and an odd way it may get of out macrophage some of the time, at least in vitro, maybe. The paper in question is: 

The Human Fungal Pathogen Cryptococcus neoformans Escapes Macrophages by a Phagosome Emptying Mechanism That Is Inhibited by Arp2/3 Complex-Mediated Actin Polymerisation by Simon A. Johnston, Robin C. May. PLoS Pathogens 6(8) e1001041.


This work follows up a really cool observation published by two groups in back to back articles in Current Biology back in 2006. Basically Cryptococcus neoformans gets into your lungs and can cause pulmonary infections. Macrophage are defensive cells of your body that are essentially cellular Pac-People that go around scarffing up foreign organisms that get into you, like C. neoformans. When I say scarf up, what I mean is the macrophage take up the microbe into a large vesicle called a phagosome, this is like the garbage disposal of the cell. What's important to remember is that the phagosome is separate from the cytoplasm of the macrophage and is effectively the surrounding environment. Generally macrophage either kill the invader or, in some cases, are killed by it, although a few disease-causing microbes can survive and grow just fine within the macrophage. C. neoformans was one of those microbes that either killed or were killed by macrophage (it is a competition, if things go well the C. neoformans is killed, if things go poorly, the macrophage is killed), or sometimes lived inside macrophage. However, in 2006 two groups published something completely different that is better seen than described.

(link in case it doesn't work for you)

What you are looking at is a big macrophage cell that contains 6-7 small C. neoformans cells within phagosomes. Around minute ~350 you'll notice the number of C. neoformans cells increases (the C. neoformans cells are dividing), and then around minute 540 something subtle happens. You may need to watch it several times to see it. Yep, all the freaking C. neoformans cells are vomited from the macrophage!!! Importantly the macrophage didn't lyse (explode) in the process. In fact, the macrophage is still alive, it divides at minute 740! That is the coolest shit eveh!

I&I 2000 paper Figure 9C. This is part of a single macrophage,
all the white glop is capsule. (The edge of the macrophage
can be seen near the bottom of the figure as the thin curvy white
area. The black box is irrelevant here.) 

Unfortunately, I was not as thrilled by this follow up paper. One big issue is that while the original observation was filled with awesomeness, there was the issue of relevance. This issue can be overlooked in the initial analysis because of the shear awesomeness. The phenomenon may be amazing to see in the laboratory under artificial conditions, but does it matter in real life, in the human host? There is a large body of literature demonstrating the ability of C. neoformans to kill macrophage. This happens by the production of massive amounts of capsule which gums up the macrophage (see figure). So while the initial observation was amazing and worth the publicity, now the question of relevance needs to be addressed.




Sadly, today's paper essentially ignored the question and went right on into determining some of the macrophage requirements for this vomiting phenomenon. I want to discuss a number of concerns that came out of our departmental journal club. (I can not take credit for all of these concerns, but I do agree with them and appreciated the discussions that arose because of them.) You should read the paper for the details as I gloss over many of them below. Plus, there is a tremendous amount of cellular biology in the paper if you are interested in cell biology. 


Concern 1. So what?

From Lab Rat
L. monocytogenes
swimming on actin

I have already noted the relevance issue regarding the phenomenon in question. This paper demonstrates that the macrophage Arp2/3 complex is important for this phenomenon as well. The authors show that actin filaments (one of the internal skeletons of a eukaryotic cell) surround phagosomes containing C. neoformans and that this requires Arp2/3. The Arp2/3 complex is required for formation of virtually all actin filaments in a cell, the notable exception being actin filaments that occur during cytokinesis. Once Arp2/3 was shown to be involved, that basically ends the story. There was no need to kill the horse it rode in on and then start beating it. Don't get me wrong it was important to show Arp2/3 was required. If Arp2/3 was not required, then that would have been interesting in its own right, as that would have been similar to what is seen for Listeria monocytogenes. L. monocytogenes, an intracellular bacterial pathogen, uses host cell actin to move around and shoot itself into neighboring cells. (While much of  L. monocytogenes motility is Arp2/3-dependent, there is Arp2/3-independent motility as well.)


Ok, once we know Arp2/3 is required, so what? It is well known that actin filaments require Arp2/3. Actin filaments also require the degradation of previously generated filament (to recycle the actin monomers) and even translation of the mRNA encoding actin. What have we actually learned here? What's the new important finding?


Concern 2. Please deal with contradictions.
In the first paragraph of the results, if you say "Long term time lapse imaging over 18 hours revealed that phagosomes containing cryptococci showed rapid, transient increases in actin-GFP fluorescence...that appeared similar to actin flashes previously seen...in macrophages loaded with latex beads [16]. " then please remember it four sentences later when you say "Notably, flashes were extremely rare on phagosomes containing latex beads (either unopsonised or IgG-opsonised) (Figure 1D)." Doesn't this seem like a discrepancy that needs to be addressed? 


Also, the results suggest that the more actin "flashes" that occur the more likely vomiting will occur (Figure 3A and B). Based on this, the prediction I would make is that drugs that promote filament formation would promote vomiting; drugs that inhibit filament formation would inhibit vomiting. Well the results of the drug experiments (Figure 4) reveal completely different data. Not a big deal, but I would expect an explanation, which was absent. (If the authors had different predictions that these results agreed with, it was not apparent to me.)


Finally, the idea the authors propose is that the phagosomal membrane gets leaky, which is why actin filaments form there. This is tested using dextran blue, a large molecular polymer of glucose linked to a blue dye. Dextran blue is taken up by macrophage along with  C. neoformans and located within the phagosome with the C. neoformans. If the phagosome becomes leaky, one expects the dextran blue to be in the cytoplasm. Well, the dextran blue does separate from the C. neoformans but it is not diffuse in the cytoplasm. The dextran blue is found in punctate spots (Figure 5), which I think could be vesicles that have separated from the major phagosome. If someone has better insights than myself, post them in the comments.


Concern 3. Philosophy of Science.
Science, at least the biological sciences, is usually based in hypothesis testing although there is a fair bit of observational science as well. When we discuss of findings, like in the discussion part of the paper, we put out our favorite ideas for what is happening (favorite ≠ best, necessarily). We sell our stuff to make it interesting to the largest audience possible. But, we also consider the limitations to our favorite ideas and even consider other possible explanations, even if we discount them shortly thereafter. We do this in writing. We do this as part of the process of being critical thinkers. I saw no evidence of this in the paper. The discussion flew right down the road of we think this, and it means that, yadda, yadda, yadda until we reach the Methods and Materials section. Part of this lack may have been due to point #1 So What? The authors may have been trying to avoid this issue being raised.


Concern 4. Conflict of interests.
Personally, I thought this work, which was labor intensive, was still quite preliminary. The data presented was generally well done, but there were a fair number of holes that, in my opinion, needed to be filled in to justify the conclusions being made. That is not to say that this paper needed any additional ducks in a row to be published. However, this paper was published in PLoS Pathogens, one of the premier journals dealing with pathogens and disease, so more ducks would be helpful. I was a little surprised...and then I saw this "One of the authors (RCM) is an editor for PLoS Pathogens". On the positive side, this is laid out clearly at the beginning of the paper as a potential conflict of interest. But I cannot help but wonder if there is some unconscious bias when one of the editors for a journal submits their paper to said journal. Yes, the manuscript was handled by a different journal editor, but these people do work together to strengthen the journal and make it successful. Do you really want to shit on a colleague who's a member of your team? I'll point out that I would not be eligible to even review a paper submitted to PLoS Pathogens if the author were also a faculty member at my university (note there are ~1500 faculty members at my university). 


Overall the paper is dealing with an interesting phenomenon, but I do think its time to determine if the phenomenon is biologically relevant. It may be possible to identify C. neoformans mutants that get vomited more or less often. If such mutants can be identified, you can see how these mutants behave in the host, which may clue you in on if/how this vomiting phenomenon contributes to colonization/infection.


(For the record, I have had a couple of papers rejected from PLoS Pathogens, which constitutes my own potential bias.)


Johnston SA, & May RC (2010). The human fungal pathogen Cryptococcus neoformans escapes macrophages by a phagosome emptying mechanism that is inhibited by Arp2/3 complex-mediated actin polymerisation. PLoS pathogens, 6 (8) PMID: 20714349

How Bacteria Swim in Your Stomach

We started our Microbiology Journal Club of the new year, technically a new decade. We started off with a bang, well a bang from a physics perspective, more of a whimper from a microbiology perspective.


The paper under discussion was:


Helicobacter pylori moves through mucus by reducing mucin viscoelasticity. by Celli JP et al. Proc Natl Acad Sci U S A. 2009 Aug 25;106(34):14321-6.

The basic premise is that H. pylori, a spiral shaped bacteria is thought to burrow its way through the gastric mucus, like a cork screw to get to the underlying epithelial cells lining your stomach. However, this work suggests another mechanism. But let's back up a little.

H. pylori - Yutaka Tsutsumi, MD

How do the epithelial cells lining your stomach survive? Great question, Im glad you asked. The epithelial cells secrete several things to protect themselves one of which is mucus. Gastric mucus has an amazing property of being able to change its viscosity. Kind of like molasses is watery when heated and almost solid when cooled. There is no decision making going on by the mucus, this is strictly a property of physics and chemistry. Now gastric mucus is interesting because it is more 'solid' the lower the pH, like 2, and more 'liquid' at higher pH, like 7. What this means is that where the mucus is exposed to acid it forms a protective shell, but closer to the epithelial cells, it is less viscous.


What does this have to do with H. pylori? Another great question. I should point out that H. pylori does not grow at pH 2, its killed by this environment much like most everything else. 

H. pylori actually modifies the local pH through an enzyme called urease that generates ammonia, which has a pH of around 12. Pretty good way to deal with stomach acid. Ill also point out that H. pylori mutants that cannot make urease are absolutely killed in the stomach. So the idea has been that H. pylori makes urease until it can burrow through the mucus to get to the epithelial cells where the pH is much more conducive to life.


But how does H. pylori burrow through the mucus when it is like a shell? That is the $64,000 question and the one considered by the authors of the paper. Remember that the viscosity of the mucus is affected by pH and that H. pylori can make the local environment less acidic. This led to the hypothesis that H. pylori increases the pH (making it less acidic), which also reduces the viscosity of the mucus (its easier to swim through) and that's how H. pylori gets through the mucus to the epithelial cells. The authors then did a number of studies to support their hypothesis, although did little to rule it out. In fact one the disappointments is that important controls were essentially non-existant and the authors could have had a much tighter more informative study if they had done them. (I should point out the paper was published in the "Biophysics and computational biology" section of PNAS not the "Microbiology" section.)


One of the first experiments done is to compare gastric mucus at pH 4 (control) with gastric mucus + H. pylori (which quickly becomes pH 7). There are two variables here, does everyone see them? The first, the one the authors care about is the presence/absence of bacteria. The second is pH. So when I see data like in Figure 1 (1B is shown), I have thoughts. 

This panel is showing the nonlinear viscoelastic response of the samples, don't worry I don't know what that means either. Regardless, the white lines, no bacteria pH 4 samples, are constant (flat) until the applied stress reaches ~10 Pa, and then they drop like a rock. The red lines, + bacteria pH 7 samples, show a different response. So the authors conclusion is that the bacteria have an effect, which I agree with. However, I want to see the data for the no bacteria pH 7 experiment (not done) or the + bacteria pH 4 experiment (not done. This latter experiment could easily be done by simply using the urease mutant, which does not increase the pH). These experiments would demonstrate whether the difference in viscoelasticity was due ONLY to the pH effect caused by the bacteria or due to the pH effect and additional effects. These bacteria also secrete proteases that could degrade the mucus, which would also reduce the viscosity.


The authors include some movies and pictures of cells and also measure some things in these datasets. However, it is really impossible to determine what is being measured or how cells were chosen. For example, one movie uses mucus at pH 4 (without urea, so the bacteria cannot change the pH) and the one bacterium shown tries real hard to swim, but doesn't go far (were there any others?). The other movie uses mucus at pH 6 and a number of bacteria, three of which move around quite well, the others do not move much at all. So when the authors are mapping the movement of bacteria (Figure 2) did they simply ignore the cells not moving? do a different experiment? what? I can't tell.


Regardless, I think the authors are on to something. I do not believe they have thrown out the burrowing model described previously. But I do believe they have refined it and made it more biologically meaningful. By looking at the true nature of gastric mucus and thinking about the bacteria in this context, I think the authors have gained some biological insights into what these bacteria need to do to survive and how the gastric mucus protects us (from acid, already known, and maybe from other bacteria, not previously known at least not via this mechanism).


Finally, I thought this work suggested something else. The model being used is that the bacteria get into your stomach, don't ask how you don't really want to know how your GI tract is colonized. The stomach is a hostile environment and the bacteria have a short time to get to safety by the epithelial cells. The bacteria secrete a bucketload of urease, increase the pH to survive a bit longer and also to reduce the viscosity of the mucus so they can swim through it to safety. Once there, the bacteria can cause chronic inflammation, which damages the epithelial cells, and can eventually lead to gastric cancer.


I suggest another possibility. The bacteria usually get in to us as infants when our stomach pH is not a acidic as it is when we are older. The bacteria survive long enough to colonize our stomachs and things go on there merry way. If the bacteria grow too much, there is sufficient reduction in the local viscosity of the mucus that acid can leak through and damage the epithelial cells (remember they don't like it either). Damage leads to inflammation and chronic damage can cause ulcers to form and eventually cancer.


These two ideas are not mutually exclusive and there is still the question why do some people get gastric illness from H. pylori and others do not.


Celli, J., Turner, B., Afdhal, N., Keates, S., Ghiran, I., Kelly, C., Ewoldt, R., McKinley, G., So, P., Erramilli, S., & Bansil, R. (2009). Helicobacter pylori moves through mucus by reducing mucin viscoelasticity Proceedings of the National Academy of Sciences, 106 (34), 14321-14326 DOI: 10.1073/pnas.0903438106

A Tangled Bank

A new, and my first, tangled bank is out over at Greg Laden's Blog. Grab a cup of joe and check it out.

Monday Journal Club...

will return next week. Last week I had to miss out and this week I presented a paper I already discussed for those who might need a fix.

Monday Journal Club: February 4th edition

Today's journal club was a discussion of the paper Self-Regulation of Candida albicans Population Size during GI Colonization." by White SJ, Rosenbach A, Lephart P, Nguyen D, Benjamin A, Tzipori S, Whiteway M, Mecsas J, and Kumamoto CA. in PLoS Pathogens 2007 Dec 7;3(12):e184.

For full disclosure I chose and presented this paper. I picked this paper for several reasons. First, I am a strong supporter of open access journals, such as PLoS pathogens so I wanted to advertise. Second, the area is of interest to me and hits on an important topic. Third, there are a couple of potential teaching points, one of which hits on a point we covered last week.

Candida albicans is a commensal (this effectively means the organism does not harm or benefit the host, although this is a point I'll try to touch on in another post) in essentially everyone. C. albicans lives throughout your digestive system including your mouth, esophagus, and intestinal tract and in the vaginal tract. C. albicans is generally well known as the causative agent of thrush (oral candidiasis) and vaginal yeast infections. It is also the primary cause of diaper rash (so antibiotic diapers generally are useless because they kill bacteria not fungi, but they market well to young mothers). However, unlike many organisms, you don't find C. albicans in the environment, in other words, C. albicans' natural niche is the human mucosa. C. albicans does infect other mammals particular in a zoo environment, however it does not appear to naturally colonize these other mammals. While mucosal infections, like thrush and vaginitis, are problematic, they are generally not life threatening. However, if C. albicans enters the bloodstream, it can disseminate to virtually every organ, including kidneys, liver, bones, heart, and brain, and kill you. This disseminated infection is called systemic candidiasis. Now these systemic infections require a host with an impaired immune system, including organ transplant patients and chemotherapy patients. Because C. albicans can cause infections if conditions are favorable, it is considered an opportunistic pathogen. What's interesting, is that the C. albicans that cause these systemic infections are the C. albicans organisms that normally reside in you gut. It is the C. albicans you are already carrying that causes these life-threatening infections. This is different from many other organisms, like E. coli, where the flora within you is generally not disease causing but variants from the environment are. Ok, long introduction to get to the main problem being addressed in this paper. We know very little about how C. albicans colonizes and grows as a commensal or how it escapes from the GI tract to the bloodstream as an opportunistic pathogen.

This paper uses a piglet model and mouse model to look at gene expression changes in C. albicans when it is in the GI tract compared to a control laboratory environment. They identify several genes including EFH1 which was expressed more in the GI tract, compared to the oral cavity or laboratory conditions. They then go on to study EFH1 in a little more detail. However, I want to point out a couple of problems I had with the aspect of the paper. First, the number of samples used was very low and only from the pig model. In fact, they only used 2 oral samples and 1 intestinal sample! An n of 1 does not a strong position make. That's not to say the results are incorrect just tenuous at best. It would have made me happier if they had also looked in the mouse GI samples to corroborate the pig data. Second, they compare the C. albicans from the pig model with laboratory grown cells. This is always going to present problems because the conditions are fundamentally different. Here, the onus is on the researchers to make things as close as possible, and I thought they fell short of the mark. For instance, the authors grew C. albicans in the laboratory at 34°C whereas the body temperature of the pig is ~39°C and the mouse is ~37°C, so there is a 3-5 degree difference (yes, this can be significant). What bothers me here is that you can grow the cells in the laboratory at whatever temperature you want trivially. So Im left wondering, what the hell? Next, they grew the cells in he laboratory in a yeast extract, bacto-peptone, sucrose solution. Not what I expect the gut of a pig or mouse has. Some alternatives could be an extract from the grain/oats/or whatever the animals are fed or an infusion from an animal source, such as beef heart (commonly used) or even pig intestine! Finally, they use logarithmically grown cells in the lab, whereas the C. albicans in the animals are almost certainly primarily in stationary phase. In fact, the authors go on to show that all but one of the genes they identified are expressed preferentially in stationary phase cells compared to logarithmically grown cells. In short, the part of the paper identified C. albicans genes expressed in the animal because C. albicans in the animal are not rapidly dividing.

The authors go on to characterize a gene called EFH1, which encodes a transcription factor of unknown function. They take a genetic approach and delete the gene and then look to see the effect. Surprisingly, they find that the efh1∆/∆ mutant colonizes the mouse intestinal tract better than the wild-type EFH1/EFH1 strain. This is surprising because we generally think more is better. Thus, we expect that wild-type C. albicans grows the best in the host and the only phenotype we would see is less growth in the host, not more. I mean how could a mutation make the cells grow better!?!?! There's lots of reasons, such as loss of this gene makes the cells grow better in this specific system (which is not relevant to the natural system), but in other important ways not addressed in this model the mutant is dead on arrival. So the positive selection observed in this model would be balanced by the strong negative selection under other conditions.

Ok, we have an interesting unexpected phenotype, what to do now? From my last journal club , you probably know the answer is a complementation test. Yes, put a wild-type copy of the EFH1 gene into the efh1∆/∆ mutant and look to see if the phenotype is restored. Well the authors did this and found that the efh1∆/∆ +EFH1 strain actuall grew worse than the wild-type strain. In other words, based on growth in the intestine of a mouse efh1∆/∆ > EFH1/EFH1 > efh1∆/∆ +EFH1. In the perfect world, you would expect efh1∆/∆ > EFH1/EFH1 = efh1∆/∆ +EFH1. So why the discrepancy? Well for one the researchers used a strong promoter to express the complementing EFH1. So the amount of EFH1 mRNA, and thus Efh1 protein, will be different. This could be the issue and is the one favored by the authors. It provides evidence that suggests the amount of Efh1 protein controls how much C. albicans growth occurs in the intestine. This is really cool!

With a really cool result comes a higher bar than would be seen with an expected result. So do the authors reach a higher bar? In my opinion no. For starters they never showed that the amount of Efh1 protein (or mRNA for that matter) is actually any different under these conditions. This seems like a fairly obvious requirement. Also, the genetics were not as rigorous as I would expect. First, they introduced their complementation construct into the endogenous locus and it didn't work. They note that others have seen this problem, which means its ok. Nice sloppy reasoning there, "others couldnt figure it out, so why should we." They also use express EFH1 from the promoter of another gene. This is often done, but its usually for a scientific reason. The authors provide no justification for this, which is odd. Finally, the strains they compare are not appropriate.
Their mutant strain has the following genotype:
arg4∆/∆ his1∆/∆ ura3∆/∆ efh1::ARG4/efh1::HIS1 leu2::URA3/LEU2. This strain is deleted for ARG4, HIS1, and URA3, two markers ARG4 and HIS1 are used to disrupt EFH1 and URA3 is introduced into the LEU2 locus to make the strain prototrophic again. Since C. albicans is diploid this strain has 1 copy of ARG4, HIS, URA3, and LEU2; 0 copies of EFH1.

Their overexpression strain has the following genotype:
arg4∆/∆ his1∆/∆ ura3∆/∆ efh1::ARG4/efh1::HIS1 adh1::P-EFH1::URA3/ADH1.
This strain is deleted for ARG4, HIS1, and URA3, two markers ARG4 and HIS1 are used to disrupt EFH1 and URA3 is introduced into the ADH1 locus along with the complementing EFH1 allele. Since C. albicans is diploid this strain has 1 copy of ARG4, HIS, URA3, ADH1, and EFH1; 2 copies of LEU2. Also, note that URA3 is expressed from different sites in the genome.

So the mutant and complemented strain they are comparing differ in EFH1 (important, this is what you are testing); LEU2 and ADH1 copy numbers and site of URA3 integration (inportant, these can confound your results since they are genetic differences). So we have the authors hypothesis Efh1 protein levels control C. albicans growth levels in the intestine. But we can consider other hypotheses, how about loss of one copy of ADH1 reduces C. albicans growth in the intestine and there is no complementation whatsoever. If we inhibit cell wall synthesis in the efh1∆/∆ mutant, growth will be reduced but that doesn't mean Efh1 protein promotes cell wall synthesis. Based on the way the experiment was done, I do not find a strong evidence that the authors actually did get any complementation. This gets back to an earlier premise I made in the first journal club, when you get unexpected or novel results, the bar is higher to ensure you are likely correct. This paper establishes some new approaches to study C. abicans intestinal colonization, but fails to reach the level of rigor to establish the surprising result that Efh1 protein controls the levels of growth of C. albicans in the intestine.

Monday Journal Club

This week our microbiology journal club discussed the paper "The cidA murein hydrolase regulator contributes to DNA release and biofilm development in Staphylococcus aureus." by Rice KC, Mann EE, Endres JL, Weiss EC, Cassat JE, Smeltzer MS, Bayles KW. published Proc Natl Acad Sci U S A. 2007 May 8;104(19):8113-8.

The main point of this paper was that CidA, a bacterial holin protein, promotes cell death which releases genomic DNA into the environment which is required for biofilm formation. I want to hit on a couple of big picture points without going into to too much detail and then focus on one aspect of the paper for teaching purposes.

First, the field of biofilm formation is, in my opinion, much like a biofilm itself.....a diffuse poorly defined thing. OK, this is not really true, but many scientists use the term so loosely as to make it meaningless. A biofilm is commonly referred to as a collection of microbes encased within an extracellular polymer. Biofilms are important medically as microbes within a biofilm are often insensitive to antibiotics and microbial biofilms can grow on catheters and artificial valves and serve as sites of continual infection/dissemination. Because the cells within the biofilm are not all uniform like what would be observed during logarithmic planktonic grown, there is heterogeneity within this structure. In fact, a biofilm could be considered analogous to a microbial tissue.

Second, programmed cell death in unicellular microbes is an interesting phenomenon/idea. However, researchers in the area of microbial programmed cell death try too hard to make it directly comparable to multi-cellular organism programmed cell death. The idea of some organisms in a population sacrificing themselves for the rest of the population is well documented and makes some sense intellectually. The idea that bacteria do it the same way as the cells in your primordial hand do it is weak to wishful thinking in my opinion.

Alright, that said, the paper. First, the authors show that wild-type cells release a cytoplasmic enzyme into the environment once they enter stationary phase (basically when they stop growing). However, cells containing a null mutation in the cidA gene do not. This demonstrates a role for CidA in cell lysis, but says nothing about biofilm formation. The authors then show several assays that demonstrate that the cidA mutant does not form a robust biofilm like wild-type cells and the authors show that extracellular DNA (presumably from lysed cells) is required for proper biofilm formation in wild-type cells. (Since cidA mutants fail to lyse there is little DNA released to help form the biofilm.) Overall this is a nice analysis that provides some insights into the role of cell lysis and DNA in biofilm formation and this analysis explains the requirement for CidA in biofilm formation.

HOWEVER, this is a simple genetic analysis paper. These type of studies are done all the time by thousands of researchers working on thousands of genes in hundreds of organisms. The authors of this study break one of the rules commandmants of molecular genetic analysis. VI. And when thoust does construct thy mutant and discover thyself an interesting phenotype, thou must proceed to carry out a complementation test or thou shalt be smiteth (Look it up, that's what the commandment says.) Now the authors know this (at least a reviewer did) and they give us this,

"Previously, we were unable to complement the antibiotic tolerance and murein hydrolase phenotypes of KB1050 (24), which was also the case in the present study, as the biofilm-defective phenotype was not complemented by supplying cidA on a plasmid (data not shown). However, this mutant phenotype is unlikely caused by a secondary site mutation because similar cidA mutations in different S. aureus genetic backgrounds also decreased their ability to form adherent biofilm (SI Fig. 7). This phenotype was also not caused by a polar effect on the downstream cid genes, because isogenic cidBC and cidC mutants grown under the same conditions produced biofilm comparable to that of UAMS-1 (data not shown)."

Let me break this down a little. When you make a genomic mutation, regardless of how you do it, there is a chance something else happened to the genomic DNA beyond what you were doing (life is a bitch). So you discover an outstanding phenotype in your mutant background...WOOHOO, contact Science, have them hold the presses.....Hold on cowboy, how do you know your mutation causes the phenotype and not some other horseshit that occurred when you made your mutant? In other words, how can you be sure the mutation and phenotype are linked? One quick and easy way, is to re-introduce a wild-type copy of the gene you mutated. The prediction (I love science) is that if the mutation causes the phenotype, putting a wild-type copy back in should rescue/restore/reverse the phenotype. If horseshit causes the phenotype, putting a wild-type copy back in will not rescue/restore/reverse the phenotype.

So, back to the authors and Im paraphrasing: our complementation tests failed for other phenotypes, and they failed for the phenotypes we present here (A, see below). We know it looks bad, but we are sure the phenotypes are not due to horseshit because when we make the mutant a bunch of times we see the same rescue (B) and other downstream genes are not required for the phenotype (C).

A. Not being able to complement one phenotype is bad, but not being able to complement a subsequent phenotype is not supportive evidence that things are working well.
B. Making the mutation a bunch of times independently does indeed tell you that the phenotype is not due to unlinked horseshit, but it could still be linked horseshit.
C. This is a little trickier. Generally bacterial genes required for a given process are found in operons, which are essentially chains of linked open reading frames (protein coding units). One or two transcriptional start sites exist to make mRNA which is then used to translate all the proteins in the operon. This allows for an efficient way to regulate all the components in a process simultaneously. So, the fact the cidB and cidC can be mutated without having an effect on biofilm formation tells us they aren't required for the phenotype. What the authors are considering is that the cidA mutation affects expression of cidB and/or cidC and that these are the true genes required for biofilm formation, not cidA. This would explain the lack of complementation because the authors add back cidA on a plasmid not in the chromosome (the authors did it right if you ask me), so if the cidA mutation disrupts cidB expression, putting the cidA gene back into the cell wouldn't help, because you still wouldn't get cidB expression.

OK, lets give the authors credit, they addressed some possible issues of horseshit. Here's one not addressed, what if the gene next to cidA (opposite cidB and cidC) is screwed up because of the cidA mutation. Let's say the mutation destroys the promoter of this hypothetical gene. You could make the cidA mutant over and over again and you would get the same phenotype that could not be complemented with cidA because this other gene would always be fucked. You could delete cidB and cidC with any affect on the phenotype. See my model fits all their data, actually mine is better because it fits all their data including the inability to complement the mutation. The authors never actually propose a model to explain this, they simply consider two possibilities and sweep the issue under the rug.

Now that being said, I still think the authors main conclusions are correct. There are many reasons to explain why you may not get complementation, although the authors failed to provide evidence for one of the reasons. However, and I think this is important, if you cannot complement your mutation, the bar is much higher to justify your conclusions. My problem is that the authors didn't consider a trivial explanation (the one I proposed) and based on my reading I expect the authors only mentioned anything regarding complementation and the lack therein in response to a reviewer. Again based on what the CidA protein does, the authors are likely correct. However, I think this paper allows us to highlight the importance of complementation testing in a rigorous molecular genetic study.

Edited for a couple of grammatical errors and to make a couple of points more clear.