Viral commitment to infection depends on host metabolism

Reviewer #1 (Public review):

In the wild, bacteria can be found in a wide range of metabolic states, including states in which they are resource-limited. Because phages heavily rely on the infected cell's molecular machinery to replicate, it is natural to wonder how phage-bacteria interactions depend on the metabolic state of the cell. In this work, Marantos et al. investigate specifically how the rate of infection of 5 different phages changes between cells grown in energy-rich conditions and cells grown in energy-depleted conditions. Their results clearly show that 4 out of the 5 phages studied display a significant reduction in infection rate in cells that are energetically depleted and provide a potential explanation for this observation by looking into the mechanisms that these phages use to irreversibly infect their host cells.

The work also tries to explain the observation using a mathematical/mechanistic model that describes infection as the sequence of two steps, where a phage first needs to bind to a cell receptor, from which it can potentially unbind, and then irreversibly infects by injecting its genome. While the model is sensible from a mechanistic perspective, the experimental evidence that supports how each model's rate is affected by the cell metabolic state is weak, as only ratios of these rates can be inferred from the data.

Reviewer #2 (Public review):

Summary:

The authors investigate the dependence of phage adsorption rates on host metabolic state, using 5 coliphages that differ in their infection cycles and host receptors. They find that four of the 5 phages showed significantly reduced infection under low metabolic states, with phages that generally have weaker adsorption being more strongly affected by low metabolism. The authors complement their findings with a 2-step infection model where phages can disengage from their hosts after initial adsorption. The paper illustrates the power of standardized experimental protocols for quantitative trait comparisons and highlights the dependence of phage infection success on host physiology.

Strengths:

The paper is well written and clearly structured.

The experiments are well-designed, and particularly commendable is the diligent use of control scenarios to allow for quantitative comparison between phages. This standardized protocol will be valuable for the entire phage community.

The authors convincingly show the impact of host physiology on phage adsorption success. This dependence has so far mainly been considered for intracellular phage replication, and the paper shows that host physiology has to be taken into account at all steps of phage infection.

Weaknesses:

There are some concerns about the experimental setup and which conclusions can be drawn from it:

Before phage infection, bacterial cultures are grown to exponential growth, washed, and then resuspended with glucose or arsenate-azide for 10min. It is however, questionable that 10 minutes is enough to simulate high and low metabolic states realistically. 10 minutes seems to be quite short to go from exponential growth to a low metabolic state, given the transcriptional memory of previous environments. It seems more likely that the population will be quite heterogeneous, with cells in various states of transition towards low metabolic states.

Given that arsenate and azide inhibit cellular metabolism, i.e., have antimicrobial effects, cells might not just downregulate metabolism but also activate the stress response, and this causes some of the observed effects on phage adsorption. Therefore, the 'low metabolic state' of the cells in this paper could mean that cells are starved or that they are stressed or both.

The abundance of receptors could change between the high and low metabolic media conditions and contribute to the observed differences in adsorption, while the authors seem to assume in their model that the initial adsorption rate always remains the same.

Reviewer #3 (Public review):

Summary:

Marantos et al. showed that for some coliphages, the energetic state of the bacterial host cell has a strong impact on whether phage infection is initiated. The authors drew this conclusion from the observation that there are more free phages remaining in the medium after infection of arsenate-azide-treated cells as compared to after infection of untreated cells. These data were analyzed and reported both as ratios of the treated vs. untreated conditions and using a mass-action kinetic model of phage-cell collision in the infection mixture. The data supported the findings that for four phages infecting Escherichia coli bacteria, namely, phages λ, 𝜙80, m13, and T6, the phages are less likely to initiate infection if the host bacteria are energy-depleted. However, for phage T5, the authors found that their infection propensity is not impacted.

Strengths:

The data presented by the authors clearly supported the principal conclusion of the study ("Viral commitment to infection depends on host metabolism"). The five phages chosen by the authors represent different viral lifestyles and infection mechanisms, highlighting the potential applicability to other Escherichia coli phages. Finally, the authors successfully used a classic mass-action model of phage-cell collision to interpret their data. The simplicity of their experimental assay, combined with the use of this mathematical model, offers other investigators who study phage-bacterial interactions in other contexts a potentially useful toolkit to examine infection in general, and specifically, the dependence of phage infection on the host's metabolic state.

Weaknesses:

(1) The authors isolated and measured the numbers of free phages in the medium after infection of bacteria under different treatments. These measurements were analyzed in two different ways: (1) simply as ratios (corrected/normalized using different controls), and (2) fitted using a simple mathematical model. I have concerns regarding both analyses.

1.1) For the first method, having different time points at which the sample of each phage is collected critically complicates data interpretation. As one incubates the phage-bacteria mixture for a longer time, more infection occurs, and the number of phages collected from the mixture decreases. Therefore, the different incubation time forfeits the goal of "a systematic and quantitative comparison across different phages [...]" (line 81), just as the authors self-criticized. Conceivably, the authors could have used the shortest measurement time for all phages (i.e., 10 minutes, as for phage λ). Alternatively, the authors could have applied a systematic criterion such as half (or any other fraction) of the latent period of each phage, which would still "maximize the incubation period while ensuring that manipulations were completed before the first infection cycle concluded" (lines 126-127). In my view, the seemingly arbitrary measurement time for each phage renders the entire first analysis very challenging to interpret. It also goes against the author's proposition that the protocol was "standardized" (line 92) or "consistent" (line 200). It is not clear what the readers are supposed to take away from this first analysis, or rather, which evidence, finding, or conclusion the manuscript would lose if the authors only presented the modeling-based analysis.

1.2) The second method of analysis sought to remove the dependence of the measurements on time. I completely agree with this goal, and the findings extracted from this analysis significantly contributed to the merits of this manuscript. However, the authors achieved this goal using a single time point for each phage to calculate the infection rate (η). As shown in Figure S3, each of the phage depletion curves is anchored by only one data point (note that the P(t)/P(0) = 1 at t = 0 is assumed, not measured). This goes against the typical way this collision model is used in the literature, where a time series is measured and used to fit the model (e.g., DOI 10.1007/978-1-60327-164-6 18, or more recently, PMID 39700139). This practice in the current manuscript reduced the robustness of the inferred η values. This problem is exacerbated by assumptions used by the authors in formulating this model. For instance, the authors used a constant value for the bacterial concentration, B, because "bacterial growth and lysis were negligible" (lines 135-136). However, considering that the bacteria were cultured at 37oC in a very rich medium (first in YT broth, then in 2% glucose), the measurement times of 20, 30, and 55 minutes are most likely one or a few generations of bacterial growth and division.

Related note: I suggest that one of the panels in Figure S3 should be moved to the main text, since it is critical to the second method of analysis.

(2) The data were able to distinguish phages that successfully infected bacteria and those that remained free in the medium, and the authors appropriately interpreted the data as such throughout the Results section. However, in the Discussion (starting from the very first sentence, line 172), the authors used terms that include "adsorption" and "entry" more interchangeably (for example, see the three sentences in lines 310-313, for "viral entry efficiency is shaped by [...]", then "adsorption kinetics modeling"). I do not see how the authors' data could distinguish between adsorption (the phage particles attaching to the outside of the cell) and entry (the phage DNA being injected into the cell). Conceivably, any phage particles that irreversibly attach to a cell but do not yet inject their genome into the cell would still be removed from the medium and therefore not quantified. Another example: in lines 189-191, the authors interpreted that "[...] when the bacterium is in a low metabolic state, the phage does not bind irreversibly to the host", but how do the authors eliminate the case of no phage binding (i.e., the reversible step) to begin with? Similarly, in lines 283-293, how do the authors delineate whether energy depletion would increase the k_off term or decrease the k_inj term, because either would result in more free phages in the medium as observed in the data? I believe that the writing of the Discussion, as it stands now, is doing a disservice to the conclusions presented in the Results section.

(3) The authors presented an argument that performing infection of all five phages in the same condition is an advantage, allowing for comparison across different phages. While this goal is a completely valid one, it is difficult to reconcile that with the fact that different phages require different optimal conditions for successful infection. For instance, phage T5 famously requires Ca2+ for successful infection into the host bacterium (and later successful replication); see PMID 13174489. However, all infections were performed in TMG, which lacks Ca2+. Perhaps the absence of T5 dependence on the host metabolism is because the infection condition used by the authors was not optimal for T5 to begin with? Similar arguments could be made for other phages.

(4) Whereas the manuscript examined five coliphages, only phage T5 and phage λ were discussed extensively. I believe some discussion points for these two phages need clarification.

4.1) Phage T5: The data obtained by the authors show that the infection rate of phage T5 is not impacted by the metabolic state of the host cell. Considering that the authors used the terms "infection", "adsorption", and "entry" interchangeably to refer to the irreversible commitment of a phage to a host cell (see point 2), this discussion regarding phage T5 lacks one critical literature context: DNA entry of phage T5 is known to occur in two phases (first-step transfer and second-step transfer). Critically, the second step can only occur if phage proteins encoded by the phage DNA transferred in the first step are expressed (see PMID 10577483 and the cited papers therein). In that context, metabolic poisoning of the host bacteria should have impeded T5 infection. The authors should comment on this point.

4.2) Phage λ: The experiment using phage λ in this current study shares many resemblances to that in Brown et al. 2022. That feature alone is not a problem, but at many places in the text, the writing is ambiguous as to whether it is discussing the results in Brown et al. 2022 or in the current manuscript. I am giving three examples below, but this is not exhaustive: (i) Lines 67-69, there is no Brown et al. 2022 reference immediately after "a mutant phage variant (λh) could bypass this dependency [...]" (not just in the previous sentence); (ii) Line 228 should clearly say "Our previous findings suggested that phage λ is capable of [...]", since it concerns Brown et al., 2022, not the current study; and (iii) Lines 245-246, there is no Brown et al., 2022 reference immediately after "we observed that a mutant variant [...] even energy-depleted host" (without a reference, it reads like the authors "observed" that finding in this current manuscript).

Also, regarding phage λ: The discussion between line 230 and line 249 is very interesting, but since it concerns the differences between λ PaPa and Ur-λ, the authors should consider mentioning and discussing a very relevant recent study, PMCID: PMC6312755.

(5) Control experiments, or references to prior studies, are needed to support that the As/Az treatment at this concentration and duration (at least 10 minutes) is sufficient to deplete the metabolic state of the cell. For instance, this can be shown by impeded or null cell growth, arrested motility (using a standard swimming assay), or a fluorescent reporter for the energetic state of the cell.