Peer review of: Bacteria evoke alarm behaviour in zebrafish (2019)

Reviewers' comments:  

Reviewer #1 (Remarks to the Author):  

This work is designed to examine the role of epidermal club cell cannibalism and bacteria in 
generating fish alarm cues. I have worked on the Schreckstoff alarm system for the majority of my 
career and I am very excited by this current work. I am in favour of publication. I am primarily a 
behavioural and evolutionary ecologist, hence my comments are restricted to that component of 
the work. I have considered all of the techniques used by the authors, but I am not an expert in 
the methods used, hence I will defer to others to address whether the techniques are appropriate.  

There are a couple of things that need to be changed prior to publication. This paper makes some 
rather bold statements in the abstract and the introduction (paragraph 2) that says there is no 
known benefit to the sender of Schreckstoff. This certainly was the case for many decades. Von 
Frisch identified fear substances in the late 1930’s and the notion of no benefit to the sender did 
not change until we published 2 papers in American Naturalist (Mathis et al. 1995 and Chivers et 
al. 1996). We showed that predators were attracted to Schreckstoff (Mathis et al. 1995) and that 
when the second predators arrived, they would often fight with the original predator, leading to 
escape of the prey (Chivers et al. 1996). This secondary predator interference was clear 
experimental evidence of a benefit to the Schreckstoff sender. Others have documented similar 
findings of attraction to alarm cues (e.g. Wisenden, Lonnstedt). It is incorrect to say there are no 
benefits to the sender. My caution that secondary predator interference may be rare in the wild 
lead me to consider that alarm cues evolved in another context (i.e that they were part of the 
innate immune system). Much of this was inspired by Iger et al. (1994; Cell and Tissue Research) 
who found photographic evidence of lymphocytes and leucocytes within club cells. The presence of 
two membranes around the lymphocytes and leucocytes indicates they were engulfed by the club 
cells, suggesting the involvement of club cells in the immune system.  
You cited my original work on this (Chivers et al. Proc B) documenting that that club cells are part 
of the immune system, but our other work (Halbgewachs et al. 2009, Biological Journal of the 
Linnean Society) was the most significant work linking alarm cells to immunity. Colin gave fathead 
minnows intraperitoneal injections of cortisol, a known immunosuppressant, or injections of a 
control substance (corn oil). He documented that fish exposed to cortisol had suppressed immune 
systems (as measured by a respiratory burst assay) and that they also reduced their investment in 
club cells. Until this current paper is published, this was the best evidence indicating that the club 
cells of Ostariophysan fishes are part of the innate immune system and that the alarm function of 
the cells evolved secondarily.  
After altering the text appropriately, I would recommend publication of this work. Congrats on a 
great study.  

Douglas P. Chivers  
Distinguished Professor  
University of Saskatchewan  

Reviewer #2 (Remarks to the Author):  

In this manuscript, Dr Jesuthasan and colleagues report that bacteria contribute to the zebrafish 
alarm response, acting synergistically with a substance from the fish. They suggest that superficial 
cells can internalise mucus and bacteria, and then invade club cells, in which the alarm substance 
(Schreckstoff) is made and stored. The authors propose that the formation of this cell-in-cell 
structure occurs through entosis and is required for the alarm response, concluding that ‘skin cell 
cannibalism and processing of bacteria generate the zebrafish fear pheromone’.  

The paper is clearly written and presented and the overall concept is of interest. I have been asked 
to provide a perspective on the data relating to cell engulfment, so will restrict my comments to 
lines 86-139, 255-270 and Figure 2. Although the notion of cell cannibalism could be interesting in 
this context, I have several major concerns, as outlined below.  

1) Does cell-in-cell formation occur?  

The authors conclude that club cells undergo cell-in-cell formation based on images in 1c, 1e and 
Fig 2.  

While many of these images could be consistent with cell internalisation, they are certainly not 
definitive. To convincingly demonstrate cell-in-cell formation, it is necessary to rigorously confirm 
that the internalised cell is inside, rather than on or adjacent to, its host.  

It would significantly strengthen these data to show:  

a) Cell-in-cell formation in 3-D. A full confocal stack of a club cell hosting another cell would help 
confirm full internalisation. This would be best visualised using a marker that clearly defines each 
cell periphery in the pair (e.g. adherens junctions or plasma membrane).  

b) An image acquired by electron microscopy to reveal how the internalised cell is housed inside 
the club cell – is there an obvious vacuole as would be expected during entosis?  

In conclusion, more robust imaging data are required to prove cell-in-cell formation here. This 
would seem achievable, particularly as the penetration of club cells by other cell types has been 
reported previously by electron microscopy (Refs 15-18).  

c) Can you explain why have more straightforward uptake mechanisms, such as transcytosis, been 
excluded as important in this context?  

2) What is the mechanism of possible cell-in-cell formation?  

Cell engulfment can proceed through a variety of mechanisms, including phagocytosis, 
emperipolesis and entosis. In their title, the authors use the term ‘cell cannibalism’, while in the 
text they infer that apparent cell-in-cell formation occurs through entosis (lines 103-114 and 
270).  

Entosis is a specific form of cell engulfment, with some key features including: 1) It is a form of 
live cell engulfment in which one viable cell is internalised into another, 2) It is a homotypic form 
of cell engulfment, occurring exclusively between paired epithelial cells, 3) Mechanistically, it 
depends upon adherens junction formation and localised actomyosin contractility (Overholtzer 
2007).  

Based on the data presented, it is unclear why the authors attribute apparent cell-in-cell formation 
to entosis, versus any other kind of engulfment? The data do not justify this conclusion, and there 
is no reason why this form of engulfment would be more likely or interesting than another.  

a) Please can you clarify whether the club cell itself bears the typical features of an epithelial cell 
required for entosis (e.g. adherens junctions)?  

b) Can you clarify whether all internalised cells are epithelial, as would be required for entosis? The 
majority of apparently internalised cells look small relative to the club cell – would this be 
expected of a superficial cell? Have you stained for an epithelial marker to be sure? Given that 
published work reports penetration of club cells by leucocytes, it would seem possible that 
heterotypic cell-in-cell formation may be occurring as well or instead (e.g. as can be seen between 

epithelial and immune human cells).  

c) Can you clarify whether the internalised cells are all live, as would be the case in entosis? Is it 
not possible that some of the examples shown could be phagocytosis of apoptotic cells?  

d) The stills shown in Fig 2a-b appear to suggest quite rapid release of bacteria into a club cell as 
it contacts a labelled neighbour (a copy of the movie would be more helpful). This would be 
unexpected with respect to entosis, in which the internalised cell is scissioned into a sealed 
vacuole, which only later undergoes lysosomal degradation.  

e) The statement in lines 105-6 that ‘entosis is characterised by a higher level of f-actin in the 
invading cell relative to the host’ is an oversimplification. What is important is spatiotemporally 
restricted activation of actomyosin contractility in the internalising cell, which pushes into its host. 
As such, a distinctive enrichment of actin, or phosphorylated myosin, can be seen specifically in 
the tail of the internalising cell (Purvanov 2014, Sun 2014). The overall intensity of actin staining 
is not very meaningful and certainly not diagnostic of entosis.  

f) The data presented on LC3B in Figures 2k-l, and discussed in lines 110-114, have been 
misinterpreted. Autophagy is a recycling process that occurs in response to various stresses and is 
characterised by the formation of autophagosomes, often visualised as LC3-positive puncta. During 
entosis, a related but quite distinct, signalling pathway degrades engulfed material. In this case, 
LC3 is recruited directly onto the entotic vacuole. This process involves transient labelling at the 
surface of this large endocytic compartment with LC3 (Florey 2011), and looks nothing like the 
image presented in Figure 2k. Moreover, during entosis, LC3 recruits in the host cell, not within 
the inner cell, as shown in 2l.  

g) Neither the actin nor LC3 data define this process as entosis. If the authors wish to explore 
entosis they should instead investigate i) a requirement for adherens junctions (Wang 2015), or ii) 
inhibition of ROCK, which has been used widely in cultured cells (Overholtzer 2007) and in vivo (Li 
2015).  

In conclusion, none of these data support the conclusion that club cells participate in entosis. The 
authors could investigate this further as suggested in point g, but should also consider other 
possible mechanisms, which would seem equally, if not more, likely.  

3) Is cell-in-cell formation required for the alarm response?  

Assuming that the authors demonstrated and defined cell-in-cell formation, the limitation remains 
that no attempt has been made to prove this process drives the alarm response. In the absence of 
experiments that manipulate cell-in-cell formation, this relationship is purely correlative.  

In the entosis field, ROCK inhibition has been used to disrupt the process and explore outcomes. 
The authors would need to do significant further work of this kind to tie any observations on cell-
in-cell formation directly to the alarm response.  

Reviewer #3 (Remarks to the Author):  

The paper describes a cell biological and molecular approach towards identification of the zebrafish 
alarm substance/Schreckstoff /fear pheromone. Karl von Frisch speculated in 1938 that an injured 
individual in a given fish shoal secretes an “alarm substance” which elicits flight behaviour in the 
other individuals. The biochemistry behind this substance and the signalling cascades involved 

remain largely unknown. The work presented by Chia Shu Ming et al is interesting not only 
because of the biochemistry involved but also because this substance seems to control social 
behaviour in fish.  

In the present study the authors report that bacteria present in or on zebrafish skin are getting 
internalized via “entosis” into club cells. There the bacteria-derived substance(s) come in contact 
with a host-derived (mucus?) substance forming the active “alarm substance”. The alarm 
substance is leaking from the club cells of one individual and then induces flight behaviour in other 
fish. For me these are early insights into a fascinating phenomenon. Some observations appear 
convincing and well supported by the data. Other observations, however, need more experimental 
support and/or better presentation to convince the referee. Here is my view:  

1. The authors show quite convincingly in Figure 3 and 4 and by using a germ-free zebrafish 
culture, that part of the alarm substance comes from one species of commensal /resident zebrafish 
bacteria, Staphylococcus sp.  
2. It is puzzling that only one species of the microbiota seems to matter. If internalization of a 
“pathogen” into club cells is due to the involvement of the innate immune machinery: what is so 
special with Staphylococcus; and why are other bacteria (eg Pseudomonas) not eliminated as 
well?
3. My major concern is the experimental set-up to prove that bacteria are internalized, that 
“entosis” is involved, and that the active substance is put together in the club cells before getting 
released via leakage. Much more work seems needed to substantiate these claims. Examples of 
major problems:
a) Fig 1a shows localization of bacteria in cells of the skin. However, the resolution of the images is 
too low to distinguish club cells from surface cells from neutrophils. The white arrow in Fig 1a 
points to a cell which is certainly not showing any label and therefore does not contain bacteria. 
Fig 1d does not convince me that we see “the cytoplasm of two club cells diffusely labelled”. To 
make their points, the authors might consider to add a scheme of fish skin to the Figure; and to 
complement the in situ hybridization images with higher resolution images including TEM.  
b) The data presented in figure 2 are also not convincing at all. Figure 2 g and h do not show a 
labelled cell within a club cell. In Fig 2k it is not clear which cells are labelled. Many cells appear to 
be labelled. Why the authors consider “diffuse label on a subset of club cells” is a mystery to me. 
Again, better images with higher resolution including EM/TEM cell would seem to me essential. (cid:3)